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CRITICISM
AND THE GROWTH OF
KNOWLEDGE

Proceedings of the International Colloquium
in the Philosophy of Science, London, 1965,
volume 4

Edited by

IMRE LAKATOS
Professor of Logic, University of London

ALAN MUSGRAVE
Professor of Philosophy, University of Otago

CAMBRIDGE
AT THE UNIVERSITY PRESS

1970

Published by the Syndics of the Cambridge University Press
Bentley House, 200 Euston Road, London N.W.1
American Branch: 32 East 57th Street, New York, N.Y. 10022

Standard Book Number: 521 07826 1

Printed in ‘Great Britain
at the University Press, Aberdeen

CONTENTS

Preface
T. S. KUHN: Logic of Discovery or Psychology of Research?

Discussion:
J. W. N. WATKINS: Against ‘Normal Science’
-&-E. TOULMIN: Does the Distinction between Normal and
Revolutionary Science Hold Water?
L. PEARCE WILLIAMS: Normal Science, Scientific Revolutions
Aad the History of Science
ae LK R. POPPER: Normal Science and its Dangers
_MARGARET MASTERMAN: The Nature of a Paradigm
, : VAKATOS: Falsification and the Methodology of Scientific
Research Programmes
_~?. K, FEYERABEND: Consolations for the Specialist
_-2T. S. KUHN: Reflections on my Critics

Index

197
231

279

PREFACE

This book constitutes the fourth volume of the Proceedings of the 1965
International Colloquium in the Philosophy of Science held at Bedford
College, Regent’s Park, London, from 11 to 17 July 1965. The Colloquium
was organized jointly by the British Society for the Philosophy of Science
and the London School of Economics and Political Science, under the
auspices of the Division of Logic, Methodology and Philosophy of Science
of the International Union of History and Philosophy of Science.

The Colloquium and the Proceedings were generously subsidized by the
sponsoring institutions, and by the Leverhulme Foundation and the
Alfred P. Sloan Foundation.

The members of the Organizing Committee were: W. C. Kneale
(Chairman), I. Lakatos (Honorary Secretary), J. W. N. Watkins (Honorary
Joint Secretary), S. Kérner, Sir Karl Popper, H. R. Post and J. O.
Wisdom.

The first three volumes of the Proceedings were published by the North-
Holland Publishing Company, Amsterdam, under the following titles:

Lakatos (ed.): Problems in the Philosophy of Mathematics, 1967.

Lakatos (ed.): The Problem of Inductive Logic, 1968.

Lakatos and Musgrave (eds.): Problems in the Philosophy of Science, 1968.

The full programme of the Colloquium is printed in the first volume of
the Proceedings.

This fourth volume follows the editorial policy pursued in the first three
volumes: it is a rational reconstruction and expansion rather than a faithful
report of the actual discussion. The whole volume arises from one sym-
posium, the one held on 13 July on Criticism and the Growth of Knowledge.
Originally, Professor Kuhn, Professor Feyerabend and Dr Lakatos were
to be the main speakers, but for different reasons (see below, p. 25) Pro-
fessor Feyerabend’s and Dr Lakatos’s contributions arrived only after the
Colloquium. Professor Watkins kindly agreed to step in in their stead.
Professor Sir Karl Popper took the chair of the lively discussion in which,
among others, Professor Stephen Toulmin, Professor Pearce Williams,
Miss Margaret Masterman and the Chairman participated.

The texts of the papers as here printed were finished at different timcs.
Professor Kuhn’s paper is printed essentially in the formin which it was
first read. The papers by Professors John Watkins, Stephen Toulmin,
Pearce Williams and Sir Karl Popper are slightly amended versions of
their original contributions. On the other hand, Miss Masterman’s paper
was finished only in 1966; while Dr Lakatos’s and Professor Feyerabend’s
papers, together with Professor Kuhn’s final reply, were finished in 1969.

vii

Vili PREFACE

The Editors—greatly assisted by Peter Clark and John Worrall—wish to
thank all the contributors for their kind cooperation. They are also grateful
to MrsChristine Jones and to Miss Mary McCormick for their conscientious
and careful work in preparing the manuscripts for publication.

THE EDITORS
London, August 1969

Logic of Discovery or Psychology
of Research?’

THOMAS 8S. KUHN
Princeton University

My object in these pages is to juxtapose the view of scientific development
outlined in my book, The Structure of Scientific Revolutions, with the
better known views of our chairman, Sir Karl Popper.? Ordinarily I should
decline such an undertaking, for I am not so sanguine as Sir Karl about the
utility of confrontations. Besides, I have admired his work for too long to
turn critic easily at this date. Nevertheless, I am persuaded that for this
occasion the attempt must be made. Even before my book was published
two and a half years ago, I had begun to discover special and often puzzling
characteristics of the relation between my views and his. That relation and
the divergent reactions I have encountered to it suggest that a disciplined
comparison of the two may produce peculiar enlightenment. Let me say
why I think this could occur.

On almost all the occasions when we turn explicitly to the same prob-
lems, Sir Karl’s view of science and my own are very nearly identical. We
are both concerned with the dynamic process by which scientific knowledge
is acquired rather than with the logical structure of the products of scien-
tific research. Given that concern, both of us emphasize, as legitimate data,
the facts and also the spirit of actual scientific life, and both of us turn
often to history to find them. From this pool of shared data, we draw many
of the same conclusions. Both of us reject the view that science progresses

‘ This paper was initially prepared at the invitation of P. A. Schilpp for his forthcoming
volume, The Philosophy of Karl R. Popper, to be published by The Open Court Publishing
Company, La Salle, Ill., in The Library of Living Philosophers, I am most grateful to
both Professor Schilpp and the publishers for permission to print it as part of the proceedings
of this symposium before its appearance in the volume for which it was first solicited.

? For purposes of the following discussion I have reviewed Sir Karl Popper’s [1959],
his [1963], and his [1957]. I have also occasionally referred to his original [1935] and his
[1945]. My own [1962] provides a more extended account of many of the issues discussed
below.

3 More than coincidence is presumably responsible for this extensive overlap. Though I
had read none of Sir Karl’s work before the appearance in 1959 of the English translation
of his [1935] (by which time my book was in draft), I had repeatedly heard a number of
his main ideas discussed. In particular, I had heard him discuss some of them as William
James Lecturer at Harvard in the spring of 1950. These circumstances do not permit me
to specify an intellectual debt to Sir Karl, but there must be one.

2 THOMAS S. KUHN

by accretion; both emphasize instead the revolutionary process by which
\ an older theory is rejected and replaced by an incompatible new one}; and
both deeply underscore the role played in this process by the older theory’s
occasional failure to meet challenges posed by logic, experiment, or oberva-
tion. Finally, Sir Karl and I are united in opposition to a number of
classical positivism’s most characteristic theses. We both emphasize, for
[example, the intimate and inevitable entanglement of scientific observa-
tion with scientific theory; we are correspondingly sceptical of efforts to
produce any neutral observation language; and we both insist that scien-
tists may properly aim to invent theories that explain observed phenomena
and that do so in terms of real objects, whatever the latter phrase may mean.
That list, though it by no means exhausts the issues about which Sir
Karl and I agree,” is already extensive enough to place us in the same
minority among contemporary philosophers of science. Presumably that
is why Sir Karl’s followers have with some regularity provided my most
sympathetic philosophical audience, one for which I continue to be grateful.
But my gratitude is not unmixed. The same agreement that evokes the
sympathy of this group too often misdirects its interest. Apparently Sir
Karl’s followers can often read much of my book as chapters from a late
(and, for some, a drastic) revision of his classic, The Logic of Scientific
Discovery. One of them asks whether the view of science outlined in my
Scientific Revolutions has not long been common knowledge. A second,
more charitably, isolates my originality as the demonstration that dis-
coveries-of-fact have a life cycle very like that displayed by innovations-of
theory. Still others express general pleasure in the book but will discuss
only the two comparatively secondary issues about which my disagreement
with Sir Karl is most nearly explicit: my emphasis on the importance of
deep commitment to tradition and my discontent with the implications of
the term ‘falsification’. All these men, in short, read my book through a
quite special pair of spectacles, and there is another way to read it. The
view through those spectacles is not wrong—my agreement with Sir Karl
is real and substantial. Yet readers outside of the Popperian circle almost

1 Elsewhere I use the term ‘paradigm’ rather than ‘theory’ to denote what is rejected
and replaced during scientific revolutions. Some reasons for the change of term will emerge
below.

2 Underlining one additional area of agreement about which there has been much
misunderstanding may further highlight what I take to be the real differences between
Sir Karl’s views and mine. We both insist that adherence to a tradition has an essential
role in scientific development. He has written, for example, ‘Quantitatively and qualitatively
by far the most important source of our knowledge—apart from inborn knowledge—is
tradition’ (Popper [1963], p. 27). Even more to the point, as early as 1948 Sir Karl wrote,
‘I do not think that we could ever free ourselves entirely from the bonds of tradition. The
so-called freeing is really only a change from one tradition to another’ ([1963], p. 122).

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 3

invariably fail even to notice that the agreement exists, and it is these
readers who most often recognize (not necessarily with sympathy) what
seem to me the central issues. I conclude that a gestalt switch divides
readers of my book into two or more groups. What one of these sees as
striking parallelism is virtually invisible to the others. The desire to under-
stand how this can be so motivates the present comparison of my view with
Sir Karl’s.

The comparison must not, however, be a mere point by point juxta-
position. What demands attention is not so much the peripheral area in
which our occasional secondary disagreements are to be isolated but the
central region in which we appear to agree. Sir Karl and I do appeal to the
same data; to an uncommon extent we are seeing the same lines on the
same paper; asked about those lines and those data, we often give virtually
identical responses, or at least responses that inevitably seem identical in
the isolation enforced by the question-and-answer mode. Nevertheless,
experiences like those mentioned above convince me that our intentions are
often quite different when we say the same things. Though the lines are
the same, the figures which emerge from them are not. That is why I call
what separates us a gestalt switch rather than a disagreement and also why
I am at once perplexed and intrigued about how best to explore the separa-
tion. How am IJ to persuade Sir Karl, who knows everything I know about
scientific development and who has somewhere or other said it, that what
he calls a duck can be seen as a rabbit? How am I to show him what it
would be like to wear my spectacles when he has already learned to look at
everything I can point to through his own?

In this situation a change in strategy is called for, and the following
suggests itself. Reading over once more a number of Sir Karl’s principal
books and essays, I encounter again a series of recurrent phrases which,
though I understand them and do not quite disagree, are locutions that [
could never have used in the same places. Undoubtedly they are most
often intended as metaphors applied rhetorically to situations for which
Sir Karl has elsewhere provided unexceptionable descriptions. Neverthe-
less, for present purposes these metaphors, which strike me as patently
inappropriate, may prove more useful than straightforward descriptions.
They may that is, be symptomatic of contextual differences that a careful
literal expression hides. If that is so, then these locutions may function
not as the lines-on-paper but as the rabbit-ear, the shawl, or the ribbon-
at-the-throat which one isolates when teaching a friend to transform his
way of seeing a gestalt diagram. That, at least, is my hope for them. I
have four such differences of locutions in mind and shall treat them

‘seriatim.

4 THOMAS S. KUHN

Among the most fundamental issues on which Sir Karl and I agree is our
insistence that an analysis of the development of scientific knowledge must
take account of the way science has actually been practiced. That being so,
a few of his recurrent generalizations startle me. One of these provides the
opening sentences of the first chapter of the Logic of Scientific Discovery:
‘A scientist’, writes Sir Karl, ‘whether theorist or experimenter, puts
forward statements, or systems of statements, and tests them step by step.
In the field of the empirical sciences, more particularly, he constructs
hypotheses, or systems of theories, and tests them against experience by
observation and experiment.”! The statement is virtually a cliché, yet in
application it presents three problems. It is ambiguous in its failure to
specify which of two sorts of ‘statements’ or ‘theories’ are being tested.
That ambiguity can, it is true, be eliminated by reference to other passages
in Sir Karl’s writings, but the generalization that results is historically
mistaken. Furthermore, the mistake proves important, for the unambig-
uous form of the description misses just that characteristic of scientific
practice which most nearly distinguishes the sciences from other creative
pursuits.

There is one sort of ‘statement’ or ‘hypothesis’ that scientists do re-
peatedly subject to systematic test. I have in mind statements of an indi-
vidual’s best guesses about the proper way to connect his own research
problem with the corpus of accepted scientific knowledge. He may, for
example, conjecture that a given chemical unknown contains the salt of a
rare earth, that the obesity of his experimental rats is due to a specified
component in their diet, or that a newly discovered spectral pattern is to be
understood as an effect of nuclear spin. In each case, the next steps in his
research are intended to try out or test the conjecture or hypothesis. If it
passes enough or stringent enough tests, the scientist has made a discovery
or has at least resolved the puzzle he had been set. If not, he must either
abandon the puzzle entirely or attempt to solve it with the aid of some other
hypothesis. Many research problems, though by no means all, take this
form. ‘Tests of this sort are a standard component of what I have elsewhere
labelled ‘normal science’ or ‘normal research’, an enterprise which accounts
for the overwhelming majority of the work done in basic science. In no usual
sense, however, are such tests directed to current theory. On the contrary,
when engaged with a normal research problem, the scientist must premise
current theory as the rules of his game. His object is to solve a puzzle,
preferably one at which others have failed, and current theory is required to

* Popper [1959], Pp. 27.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 5

define that puzzle and to guarantee that, given sufficient brilliance, it can
be solved.! Of course the practitioner of such an enterprise must often test
the conjectural puzzle solution that his ingenuity suggests. But only his
personal conjecture is tested. If it fails the test, only his own ability not the
corpus of current science is impugned. In short, though tests occur fre-
quently in normal science, these tests are of a peculiar sort, for in the final
analysis it is the individual scientist rather than current theory which is
tested.

This is not, however, the sort of test Sir Karl has in mind. He is above
all concerned with the procedures through which science grows, and he is
convinced that ‘growth’ occurs not primarily by accretion but by the
revolutionary overthrow of an accepted theory and its replacement by a
better one.? (The subsumption under ‘growth’ of ‘repeated overthrow’ is
itself a linguistic oddity whose raison d’étre may become more visible as
we proceed.) Taking this view, the tests which Sir Karl emphasizes are
those which were performed to explore the limitations of accepted theory
or to subject a current theory to maximum strain. Among his favourite
examples, all of them startling and destructive in their outcome, are
Lavoisier’s experiments on calcination, the eclipse expedition of 1919,
and the recent experiments on parity conservation.’ All, of course, are
classic tests, but in using them to characterize scientific activity Sir Karl
misses something terribly important about them. Episodes like these are
very rare in the development of science. When they occur, they are gen-
erally called forth either by a prior crisis in the relevant field (Lavoisier’s
experiments or Lee and Yang’s*) or by the existence of a theory which
competes with the existing canons of research (Einstein’s general relativity).
These are, however, aspects of or occasions for what I have elsewhere
called ‘extraordinary research’, an enterprise in which scientists do display

1 For an extended discussion of normal science, the activity which practitioners are
trained to carry on, see my [1962], pp. 23-42, and 135-42. It is important to notice that
when I describe the scientist as a puzzle solver and Sir Karl describes him as a problem
solver (e.g. in his [1963], pp. 67, 222), the similarity of our terms disguises a fundamental
divergence. Sir Karl writes (the italics are his), ‘Admittedly, our expectations, and thus our
theories, may precede, historically, even our problems. Yet science starts only with problems.
Problems crop up especially when we are disappointed in our expectations, or when our
theories involve us in difficulties, in contradictions’. I use the term ‘puzzle’ in order to
emphasize that the difficulties which ordinarily confront even the very best scientists are,
like crossword puzzles or chess puzzles, challenges only to his ingenuity. He is in difficulty,
not current theory. My point is almost the converse of Sir Karl’s.

2 Cf. Popper [1963], pp. 129, 215 and 221, for particularly forceful statements of this
position. ;

3 For example, Popper [1963], p. 220.

4 For the work on calcination see, Guerlac [1961]. For the background of the parity
experiments see, Hafner and Presswood [1965].

6 THOMAS Ss. KUHN

very many of the characteristics Sir Kar] emphasizes, but one which, at
least in the past, has arisen only intermittently and under quite special
circumstances in any scientific speciality.

I suggest then that Sir Karl has characterized the entire scientific
enterprise in terms that apply only to its occasional revolutionary parts.
His emphasis is natural and common: the exploits of a Copernicus or
Einstein make better reading than those of a Brahe or Lorentz; Sir Karl
would not be the first if he mistook what I call normal science for an
intrinsically uninteresting enterprise. Nevertheless, neither science nor
the development of knowledge is likely to be understood if research is
viewed exclusively through the revolutions it occasionally produces. For
example, though testing of basic commitments occurs only in extra-
ordinary science, it is normal science that discloses both the points to test
and the manner of testing. Or again, it is for the normal, not the extra-
ordinary practice of science that professionals are trained; if they are
nevertheless eminently successful in displacing and replacing the theories
on which normal practice depends, that is an oddity which must be ex-
plained. Finally, and this is for now my main point, a careful look at the
scientific enterprise suggests that it is normal science, in which Sir Karl’s
sort of testing does not occur, rather than extraordinary science which
most nearly distinguishes science from other enterprises. If a demarcation
criterion exists (we must not, I think, seek a sharp or decisive one), it may
lie just in that part of science which Sir Karl ignores.

In one of his most evocative essays, Sir Karl traces the origin of ‘the
tradition of critical discussion [which] represents the only practicable way
of expanding our knowledge’ to the Greek philosophers between Thales
and Plato, the men who, as he sees it, encouraged critical discussion both
between schools and within individual schools.? The accompanying de-
scription of Presocratic discourse is most apt, but what is described does
not at all resemble science. Rather it is the tradition of claims, counter-
claims, and debates over fundamentals which, except perhaps during the
Middle Ages, have characterized philosophy and much of social science
ever since. Already by the Hellenistic period mathematics, astronomy,
statics and the geometric parts of optics had abandoned this mode of dis-
course in favour of puzzle solving. Other sciences, in increasing numbers,
have undergone the same transition since. In a sense, to turn Sir Karl’s
view on its head, it is precisely the abandonment of critical discourse that
marks the transition to a science. Once a field has made that transition,
critical discourse recurs only at moments of crisis when the bases of the

1 The point is argued at length in my [1962], pp. 52-97-
2 Popper [1963], chapter 5, especially pp. 148-52.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 7

field are again in jeopardy.1 Only when they must choose between com-
peting theories do scientists behave like philosophers. That, I think, is
why Sir Karl’s brilliant description of the reasons for the choice between
metaphysical systems so closely resembles my description of the reasons
for choosing between scientific theories.? In neither choice, as I shall
shortly try to show, can testing play a quite decisive role.

There is, however, good reason why testing has seemed to do so, and in
exploring it Sir Karl’s duck may at last become my rabbit. No puzzle-
solving enterprise can exist unless its practitioners share criteria which,
for that group and for that time, determine when a particular puzzle has
been solved. The same criteria necessarily determine failure to achieve a
solution, and anyone who chooses may view that failure as the failure of a
theory to pass a test. Normally, as I have already insisted, it is not viewed
that way. Only the practitioner is blamed, not his tools. But under the
special circumstances which induce a crisis in the profession (e.g. gross
failure, or repeated failure by the most brilliant professionals) the group’s
opinion may change. A failure that had previously been personal may then
come to seem the failure of a theory under test. Thereafter, because the test
arose from a puzzle and thus carried settled criteria of solution, it proves
both more severe and harder to evade than the tests available within a
tradition whose normal mode is critical discourse rather than puzzle solving.

In a sense, therefore, severity of test-criteria is simply one side of the
coin whose other face is a puzzle-solving tradition. That is why Sir Karl’s
line of demarcation and my own so frequently coincide. That coincidence
is, however, only in their outcome; the process of applying them is very
different, and it isolates distinct aspects of the activity about which the
decision—science or non-science—is to be made. Examining the vexing
cases, for example, psychoanalysis or Marxist historiography, for which
Sir Karl tells us his criterion was initially designed,? I concur that they
cannot now properly be labelled ‘science’. But I reach that conclusion by a
route far surer and more direct than his. One brief example may suggest
that of the two criteria, testing and puzzle solving, the latter is at once the
less equivocal and the more fundamental.

To avoid irrelevant contemporary controversies, I consider astrology
rather than, say, psychoanalysis. Astrology is Sir Karl’s most frequently
cited example of a ‘pseudo-science’.* He says: ‘By making their interpreta-
tions and prophecies sufficiently vague they [astrologers] were able to

1 Though I was not then seeking a demarcation criterion, just these points are argued
at length in my [1962], pp. 10-22 and 87-90.

2 Cf. Popper [1963], pp. 192-200, with my [1962], pp. 143-58. * Popper [1963], p. 34.

4 The index to Popper [1963] has eight entries under the heading ‘astrology as a typical
pseudo science’.

8 THOMAS 8S. KUHN

explain away anything that might have been a refutation of the theory had
the theory and the prophecies been more precise. In order to escape falsi-
fication they destroyed the testability of the theory.’! Those generalizations
catch something of the spirit of the astrological enterprise. But taken at all
literally, as they must be if they are to provide a demarcation criterion,
they are impossible to support. The history of astrology during the cen-
turies when it was intellectually reputable records many predictions that
categorically failed. Not even astrology’s most convinced and vehement
exponents doubted the recurrence of such failures. Astrology cannot be
barred from the sciences because of the form in which its predictions were
cast.

Nor can it be barred because of the way its practitioners explained
failure. Astrologers pointed out, for example, that, unlike general pre-
dictions about, say, an individual’s propensities or a natural calamity, the
forecast of an individual’s future was an immensely complex task, demand-
ing the utmost skill, and extremely sensitive to minor errors in relevant
data. The configuration of the stars and eight planets was constantly
changing; the astronomical tables used to compute the configuration at an
individual’s birth were notoriously imperfect; few men knew the instant
of their birth with the requisite precision.? No wonder, then, that fore-
casts often failed. Only after astrology itself became implausible did these
arguments come to seem question-begging.4 Similar arguments are regu-
larly used today when explaining, for example, failures in medicine or
meteorology. In times of trouble they are also deployed in the exact
sciences, fields like physics, chemistry, and astronomy.® There was nothing
unscientific about the astrologer’s explanation of failure.

Nevertheless, astrology was not a science. Instead it was a craft, one of
the practical arts, with close resemblances to engineering, meteorology,
and medicine as these fields were practised until little more than a century
ago. The parallels to an older medicine and to contemporary psycho-
analysis are, I think, particularly close. In each of these fields shared theory
was adequate only to establish the plausibility of the discipline and to
provide a rationale for the various craft-rules which governed practice.
These rules had proved their use in the past, but no practitioner supposed
they were sufficient to prevent recurrent failure. A more articulated theory
and more powerful rules were desired, but it would have been absurd to

* Popper [1963], p. 37.

2 For examples see, Thorndike [1923-58], 5, pp. 225 ff.;°6, pp. 71, IOI, 114.

3 For reiterated explanations of failure see, ibid. 1, pp. 11 and 514 f.; 4, 368; 5, 279.

* A perceptive account of some reasons for astrology’s loss of plausibility is included in

Stahlman [1956]. For an explanation of astrology’s previous appeal see, Thorndike [1955].
5 Cf. my [1962], pp. 66-76.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 9

abandon a plausible and badly needed discipline with a tradition of limited
success simply because these desiderata were not yet at hand. In their
absence, however, neither the astrologer nor the doctor could do research.
Though they had rules to apply, they had no puzzles to solve and there-
fore no science to practise.

Compare the situations of the astronomer and the astrologer. If an
astronomer’s prediction failed and his calculations checked, he could hope
to set the situation right. Perhaps the data were at fault: old observations
could be re-examined and new measurements made, tasks which posed a
host of calculational and instrumental puzzles. Or perhaps theory needed
adjustment, either by the manipulation of epicycles, eccentrics, equants,
etc., or by more fundamental reforms of astronomical technique. For more
than a millennium these were the theoretical and mathematical puzzles
around which, together with their instrumental counterparts, the astrono-
mical research tradition was constituted. The astrologer, by contrast, had
no such puzzles. The occurrence of failures could be explained, but par-
ticular failures did not give rise to research puzzles, for no man, however
skilled, could make use of them in a constructive attempt to revise the
astrological tradition. There were too many possible sources of difficulty,
most of them beyond the astrologer’s knowledge, control, or responsi-
bility. Individual failures were correspondingly uninformative, and they
did not reflect on the competence of the prognosticator in the eyes of his
professional compeers.? Though astronomy and astrology were regularly
practised by the same people, including Ptolemy, Kepler, and Tycho
Brahe, there was never an astrological equivalent of the puzzle-solving
astronomical tradition. And without puzzles, able first to challenge and
then to attest the ingenuity of the individual practitioner, astrology could

1 This formulation suggests that Sir Karl’s criterion of demarcation might be saved by a
minor restatement entirely in keeping with his apparent intent. For a field to be a science its
conclusions must be logically derivable from shared premises. On this view astrology is
to be barred not because its forecasts were not testable but because only the most general
and least testable ones could be derived from accepted theory. Since any field that did satisfy
this condition might support a puzzle solving tradition, the suggestion is clearly helpful.
It comes close to supplying a sufficient condition for a field’s being a science. But in this
form, at least, it is not even quite a sufficient condition, and it is surely not a necessary one.
It would, for example, admit surveying and navigation as sciences, and it would bar taxo-
nomy, historical geology, and the theory of evolution. The conclusions of a science may be
both precise and binding without being fully derivable by logic from accepted premises,
Cf. my [1962], pp. 35-51, and also the discussion in Section III, below.

2 This is not to suggest that astrologers did not criticize each other. On the contrary, like
practitioners of philosophy and some social sciences, they belonged to a variety of different
schools, and the inter-school strife was sometimes bitter. But these debates ordinarily
revolved about the implausibility of the particular theory employed by one or another
school. Failures of individual predictions played very little role. Compare Thorndike

[1923-58], 5, P. 233.

10 THOMAS S. KUHN

not have become a science even if the stars had, in fact, controlled human
destiny.

In short, though astrologers made testable predictions and recognized
that these predictions sometimes failed, they did not and could not engage
in the sorts of activities that normally characterize all recognized sciences.
Sir Karl is right to exclude astrology from the sciences, but his over-con-
centration on science’s occasional revolutions prevents his seeing the surest
reason for doing so.

That fact, in turn, may explain another oddity of Sir Karl’s historio-
graphy. Though he repeatedly underlines the role of tests in the replace-
ment of scientific theories, he is also constrained to recognize that many
theories, for example the Ptolemaic, were replaced before they had in fact
been tested. On some occasions, at least, tests are not requisite to the
revolutions through which science advances. But that is not true of puzzles.
Though the theories Sir Karl cites had not been put to the test before
their displacement, none of these was replaced before it had ceased ade-
quately to support a puzzle-solving tradition. The state of astronomy was a
scandal in the early sixteenth century. Most astronomers nevertheless felt
that normal adjustments of a basically Ptolemaic model would set the
situation right. In this sense the theory had not failed a test. But a few
astronomers, Copernicus among them, felt that the difficulties must lie in
the Ptolemaic approach itself rather than in the particular versions of
Ptolemaic theory so far developed, and the results of that conviction are
already recorded. The situation is typical.? With or without tests, a puzzle-
solving tradition can prepare the way for its own displacement. To rely
on testing as the mark of a science is to miss what scientists mostly do and,
with it, the most characteristic feature of their enterprise.

With the background supplied by the preceding remarks we can quickly
discover the occasion and consequences of another of Sir Karl’s favourite
locutions. The preface to Conjectures and Refutations opens with the sen-
tence: “The essays and lectures of which this book is composed, are varia-
tions upon one very simple theme—the thesis that we can learn from our
mistakes.’ The emphasis is Sir Karl’s; the thesis recurs in his writing from
an early date*; taken in isolation, it inevitably commands assent. Everyone

1 Cf. Popper [1963], p. 246. 2 Cf. my [1962], pp. 77-87.

3 'The quotation is from Popper [1963], p. vii, in a preface dated 1962. Earlier Sir Karl
had equated ‘learning from our mistakes’ with ‘learning hy trial and error’ ([1963], p. 216),
and the trial-and-error formulation dates from at least 1937 ({1963], p. 312) and is in

spirit older than that. Much of what is said below about Sir Karl’s notion of ‘mistake’
applies equally to his concept of ‘error’.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? Il

can and does learn from his mistakes; isolating and correcting them is an
essential technique in teaching children. Sir Karl’s rhetoric has roots in
everyday experience. Nevertheless, in the contexts for which he invokes
this familiar imperative, its applications seems decisively askew. I am not
sure a mistake has been made, at least not a mistake to learn from.

One need not confront the deeper philosophical problems presented by
mistakes to see what is presently at issue. It is a mistake to add three plus
three and get five, or to conclude from ‘All men are mortal’ to ‘All mortals
are men’. For different reasons, it is a mistake to say, ‘He is my sister’, or
to report the presence of a strong electric field when test charges fail to
indicate it. Presumably there are still other sorts of mistakes, but all the
normal ones are likely to share the following characteristics. A mistake is
made, or is committed, at a specifiable time and place by a particular
individual. That individual has failed to obey some established rule of
logic, or of language, or of the relations between one of these and ex-
perience. Or he may instead have failed to recognize the consequences of a
particular choice among the alternatives which the rules allow him. The
individual can learn from his mistake only because the group whose prac-
tice embodies these rules can isolate the individual’s failure in applying
them. In short, the sorts of mistakes to which Sir Karl’s imperative most
obviously applies are in individual’s failure of understanding or of recog-
nition within an activity governed by pre-established rules. In the sciences
such mistakes occur most frequently and perhaps exclusively within the
practice of normal puzzle-solving research.

That is not, however, where Sir Karl seeks them, for his concept of
science obscures even the existence of normal research. Instead, he looks
to the extraordinary or revolutionary episodes in scientific development.
The mistakes to which he points are not usually acts at all but rather out-
of-date scientific theories: Ptolemaic astronomy, the phlogiston theory, or
Newtonian dynamics, and ‘learning from our mistakes’ is, correspondingly,
what occurs when a scientific community rejects one of these theories and
replaces it with another. If this does not immediately seem an odd usage,

1 Popper [1963], pp. 215 and 220. In these pages Sir Karl outlines and illustrates his
thesis that science grows through revolutions. He does not, in the process, ever juxtapose
the term ‘mistake’ with the name of an out-of-date scientific theory, presumably because his
sound historic instinct inhibits so gross an anachronism. Yet the anachronism is funda-
mental to Sir Karl’s rhetoric, which does repeatedly provide clues to more substantial
differences between us. Unless out-of-date theories are mistakes, there is no way to reconcile,
say, the opening paragraph of Sir Karl's preface ([1963], p. vii: ‘learn from our mistakes’;
‘our often mistaken attempts to solve our problems’; ‘tests which may help us in the dis-
covery of our mistakes’) with the view ([1963], p. 215) that ‘the growth of scientific know-
ledge ... [consists in] the repeated overthrow of scientific theories and their replacement
by better or more satisfactory ones’.

12 THOMAS S. KUHN

that is mainly because it appeals to the residual inductivist in us all.
Believing that valid theories are the product of correct inductions from
facts, the inductivist must also hold that a false theory is the result of a
mistake in induction. In principle, at least, he is prepared to answer the
questions: what mistake was made, what rule broken, when and by whom,
in arriving at, say, the Ptolemaic system? To the man for whom those are
sensible questions and to him alone, Sir Karl’s locution presents no
problems.

But neither Sir Karl nor I is an inductivist. We do not believe that there
are rules for inducing correct theories from facts, or even that theories,
correct or incorrect, are induced at all. Instead we view them as imagi-
native posits, invented in one piece for application to nature. And though
we point out that such posits can and usually do at last encounter puzzles
they cannot solve, we also recognize that those troublesome confrontations
rarely occur for some time after a theory has been both invented and
accepted. In our view, then, no mistake was made in arriving at the
Ptolemaic system, and it is therefore difficult for me to understand what
Sir Karl has in mind when he calls that system, or any other out-of-date
theory, a mistake. At most one may wish to say that a theory which was not
previously a mistake has become one or that a scientist has made the mistake
of clinging to a theory for too long. And even these locutions, of which at
least the first is extremely awkward, do not return us to the sense of mistake
with which we are most familiar. Those mistakes are the normal ones which
a Ptolemaic (or a Copernican) astronomer makes within his system, per-
haps in observation, calculation, or the analysis of data. They are, that is,
the sort of mistake which can be isolated and then at once corrected,
leaving the original system intact. In Sir Karl’s sense, on the other hand, a
mistake infects an entire system and can be corrected only by replacing
the system as a whole. No locutions and no similarities can disguise these
fundamental differences, nor can it hide the fact that before infection set
in the system had the full integrity of what we now call sound know-
ledge.

Quite possibly Sir Karl’s sense of ‘mistake’ can be salvaged, but a
successful salvage operation must deprive it of certain still current implica-
tions. Like the term ‘testing’, ‘mistake’ has been borrowed from normal
science, where its use is reasonably clear, and applied to revolutionary
episodes, where its application is at best problematic. That transfer creates,
or at least reinforces, the prevalent impression that whole theories can be
judged by the same sort of criteria that one employs when judging a
theory’s individual research applications. The discovery of applicable
criteria then becomes a primary desideratum for many people. That Sir

LOGIC OF DISCOVERY OF PSYCHOLOGY OF RESEARCH? 13

Karl should be among them is strange, for the search runs counter to the
most original and fruitful thrust in his philosophy of science. But I can
understand his methodological writings since the Logik der Forschung in
no other way. I shall now suggest that he has, despite explicit disclaimers,
consistently sought evaluation procedures which can be applied to theories
with the apodictic assurance characteristic of the techniques by which one
identifies mistakes in arithmetic, logic, or measurement. I fear that he is
pursuing a will-o’-the-wisp born from the same conjunction of normal and
extraordinary science which made tests seem so fundamental a feature of
the sciences.

In his Logtk der Forschung, Sir Karl underlined the asymmetry of a gen-
eralization and its negation in their relation to empirical evidence. A
scientific theory cannot be shown to apply successfully to all its possible
instances, but it can be shown to be unsuccessful in particular applica-
tions. Emphasis upon that logical truism and its implications seems to me
a forward step from which there must be no retreat. The same asymmetry
plays a fundamental role in my Structure of Scientific Revolutions, where a
theory’s failure to provide rules that identify solvable puzzles is viewed as
the source of professional crises which often result in the theory’s being
replaced. My point is very close to Sir Karl’s, and I may well have taken
it from what I had heard of his work.

But Sir Karl describes as ‘falsification’ or ‘refutation’ what happens
when a theory fails in an attempted application, and these are the first of a
series of related locutions that again strike me as extremely odd. Both
‘falsification’ and ‘refutation’ are antonyms of ‘proof’. They are drawn
principally from logic and from formal mathematics; the chains of argu-
ment to which they apply end with a ‘Q.E.D.’; invoking these terms implies
the ability to compel assent from any member of the relevant professional
community. No member of this audience, however, still needs to be told
that, where a whole theory or often even a scientific law is at stake, argu-
ments are seldom so apodictic. All experiments can be challenged, either
as to their relevance or their accuracy. All theories can be modified by a
variety of ad hoc adjustments without ceasing to be, in their main lines, the
same theories. It is important, furthermore, that this should be so, for it
is often by challenging observations or adjusting theories that scientific
knowledge grows. Challenges and adjustments are a standard part of
normal research in empirical science, and adjustments, at least, play a
dominant role in informal mathematics as well. Dr Lakatos’s brilliant
analysis of the permissible rejoinders to mathematical refutations

14 THOMAS S. KUHN

provides the most telling arguments I know against a naive falsificationist
position.!

Sir Karl is not, of course, a naive falsificationist. He knows all that has
just been said and has emphasized it from the beginning of his career. Very
early in his Logic of Scientific Discovery, for example, he writes: ‘In point
of fact, no conclusive disproof of a theory can ever be produced; for it is
always possible to say that the experimental results are not reliable or that
the discrepancies which are asserted to exist between the experimental
results and the theory are only apparent and that they will disappear with
the advance of our understanding.’® Statements like these display one
more parallel between Sir Karl’s view of science and my own, but what we
make of them could scarcely be more different. For my view they are
fundamental, both as evidence and as source. For Sir Karl’s, in contrast,
they are an essential qualification which threatens the integrity of his basic
position. Having barred conclusive disproof, he has provided no substitute
for it, and the relation he does employ remains that of logical falsification.
Though he is not a naive falsificationist, Sir Karl may, I suggest, legiti-
mately be treated as one.

If his concern were exclusively with demarcation, the problems posed by
the unavailability of conclusive disproofs would be less severe and perhaps
eliminable. Demarcation might, that is, be achieved by an exclusively
syntactic criterion.® Sir Karl’s view would then be, and perhaps is, that a
theory is scientific if and only if observation statements—particularly the
negations of singular existential statements—can be logically deduced
from it, perhaps in conjunction with stated background knowledge. The
difficulties (to which I shall shortly turn) in deciding whether the outcome
of a particular laboratory operation justifies asserting a particular observa-
tion statement would then be irrelevant. Perhaps, though the basis for
doing so is less apparent, the equally grave difficulties in deciding whether
an observation statement deduced from an approximate (e.g. mathemati-
cally manageable) version of the theory should be considered conse-
quences of the theory itself could be eliminated in the same way. Problems
like these would belong not to the syntactics but to the pragmatics or
semantics of the language in which the theory was cast, and they would
therefore have no role in determining its status as a science. To be scien-
tific a theory need be falsifiable only by an observation statement not by
actual observation. The relation between statements, unlike that between

1 Lakatos [1963-4]. 2 Popper [1959], p. 50.

3 Though my point is somewhat different, I owe my recognition of the need to confront
this issue to C. G. Hempel’s strictures on those who misinterpret Sir Karl by attributing
to him a belief in absolute rather than relative falsification. See his [1965], p. 45. I am
also indebted to Professor Hempel for a close and perceptive critique of this paper in draft.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 15

a statement and an observation, could be the conclusive disproof familiar
from logic and mathematics.

For reasons suggested above (p. 9, footnote 1) and elaborated immed-
iately below, I doubt that scientific theories can without decisive change be
cast in a form which permits the purely syntactic judgements which this
version of Sir Karl’s criterion requires. But even if they could, these re-
constructed theories would provide a basis only for his demarcation cri-
terion, not for the logic of knowledge so closely associated with it. The
latter has, however, been Sir Karl’s most persistent concern, and his
notion of it is quite precise. “The logic of knowledge... ,’ he writes,
‘consists solely in investigating the methods employed in those system-
atic tests to which every new idea must be subjected if it is to be seriously
entertained.’! From this investigation, he continues, result methodological
rules or conventions like the following: ‘Once a hypothesis has been pro-
posed and tested, and has proved its mettle, it may not be allowed to drop
out without “good reason’’. A “good reason” may be, for instance . . . the
falsification of one of the consequences of the hypothesis.”?

Rules like these, and with them the entire logical enterprise described
above, are no longer simply syntactic in their import. They require that both
the epistemological investigator and the research scientist be able to relate
sentences derived from a theory not to other sentences but to actual obser-
vations and experiments. This is the context in which Sir Karl’s term
‘falsification’ must function, and Sir Karl is entirely silent about how it
can do so. What is falsification if it is not conclusive disproof? Under what
circumstances does the logic of knowledge require a scientist to abandon a
previously accepted theory when confronted, not with statements about
experiments, but with experiments themselves? Pending clarification of
these questions, I am not clear that what Sir Karl has given us is a logic of
knowledge at all. In my conclusion I shall suggest that, though equally
valuable, it is something else entirely. Rather than a logic, Sir Karl has
provided an ideology; rather than methodological rules, he has supplied
procedural maxims.

That conclusion must, however, be postponed until after a last deeper
look at the source of the difficulties with Sir Karl’s notion of falsification.
It presupposes, as I have already suggested, that a theory is cast, or can
without distortion be recast, in a form which permits scientists to classify
each conceivable event as either a confirming instance, a falsifying in-
stance, or irrelevant to the theory. That is obviously required if a general
law is to be falsifiable: to test the generalization (x) ¢ (x) by applying it to
the constant a, we must be able to tell whether or not a lies within the

Popper [1959], p- 31- * Popper [1959], pp. $3 f.

16 THOMAS 8S. KUHN

range of the variable x and whether or not ¢ (a). The same presupposition
is even more apparent in Sir Karl’s recently elaborated measure of veri-
similitude. It requires that we first produce the class of all logical conse-
quences of the theory and then choose from among these, with the aid of
background knowledge, the classes of all true and of all false consequences.
At least, we must do this if the criterion of verisimilitude is to result in a
method of theory choice. None of these tasks can, however, be accomplished
unless the theory is fully articulated logically and unless the terms through
which it attaches to nature are sufficiently defined to determine their
applicability in each possible case. In practice, however, no scientific theory
satisfies these rigorous demands, and many people have argued that a
theory would cease to be useful in research if it did so.? I have myself else-
where introduced the term ‘paradigm’ to underscore the dependence of
scientific research upon concrete examples that bridge what would other-
wise be gaps in the specification of the content and application of scien-
tific theories. The relevant arguments cannot be repeated here. But a brief
example, though it will temporarily alter my mode of discourse, may be
even more useful.

My example takes the form of a constructed epitome of some elementary
scientific knowledge. That knowledge concerns swans, and to isolate its
presently relevant characteristics I shall ask three questions about it: (a)
How much can one know about swans without introducing explicit
generalizations like ‘All swans are white’? (6) Under what circumstances
and with what consequences are such generalizations worth adding to
what was known without them? (c) Under what circumstances are general-
izations rejected once they have been made? In raising these questions my
object is to suggest that, though logic is a powerful and ultimately an
essential tool of scientific enquiry, one can have sound knowledge in forms
to which logic can scarcely be applied. Simultaneously, I shall suggest
that logical articulation is not a value for its own sake, but is to be under-
taken only when and to the extent that circumstances demand it.

Imagine that you have been shown and can remember ten birds which
have authoritatively been identified as swans; that you have a similar
acquaintance with ducks, geese, pigeons, doves, gulls, etc.; and that you
are informed that each of these types constitutes a natural family. A
natural family you already know as an observed cluster of like objects,

1 Popper [1963], pp. 233-5. Notice also, at the foot of the last of these pages, that Sir
Karl’s comparison of the relative verisimilitude of two theories depends upon there being
‘no revolutionary changes in our background knowledge’, an assumption which he no-
where argues and which is hard to reconcile with his conception of scientific change by

revolutions.
2 Braithwaite [1953], pp. 50-87, especially p. 76, and my [1962], pp. 97-101.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 17

sufficiently important and sufficiently discrete to command a generic
name. More precisely, though here I introduce more simplification than
the concept requires, a natural family is a class whose members resemble
each other more closely than they resemble the members of other natural
families.1 The experience of generations has to date confirmed that all
observed objects fall into one or another natural family. It has, that is,
shown that the entire population of the world can always be divided (though
not once and for all) into perceptually discontinuous categories. In the per-
ceptual spaces between these categories there are believed to be no objects
at all.

What you have learned about swans from exposure to paradigms is very
much like what children first learn about dogs and cats, tables and chairs,
mothers and fathers. Its precise scope and content are, of course, impossible
to specify, but it is sound knowledge nonetheless. Derived from observa-
tion, it can be infirmed by further observation, and it meanwhile provides a
basis for rational action. Seeing a bird much like the swans you already
know, you may reasonably presume that it will require the same food as
the others and will breed with them. Provided swans are a natural family,
no bird which closely resembles them on sight should display radically
different characteristics on closer acquaintance. Of course you may have
been misinformed about the natural integrity of the swan family. But that
can be discovered from experience, for example, by the discovery of a
number of animals (note that more than one is required) whose character-
istics bridge the gap between swans and, say, geese by barely perceptible
intervals.? Until that does occur, however, you will know a great deal about
swans though you will not be altogether sure what you know or what a
swan is.

Suppose now that all the swans you have actually observed are white.
Should you embrace the generalization, ‘All swans are white’? Doing so
will change what you know very little; that change will be of use only in
the unlikely event that you meet a non-white bird which otherwise re-
sembles a swan; by making the change you increase the risk that the swan

1 Note that the resemblance between members of a natural family is here a learned re-
lationship and one which can be unlearned. Contemplate the old saw, “To an occidental,
all chinamen look alike’. That example also highlights the most drastic of the simplifications
introduced at this point. A fuller discussion would have to allow for hierarchies of natural
families with resemblance relations between families at the higher levels.

2 This experience would not necessitate the abandonment of either the category ‘swans’
or the category ‘geese’, but it would necessitate the introduction of an arbitrary boundary
between them. The families ‘swans’ and ‘geese’ would no longer be natural families, and
you could conclude nothing about the character of a new swan-like bird that was not also

true of geese. Empty perceptual space is essential if family membership is to have cognitive
content,

18 THOMAS S. KUHN

family will prove not to be a natural family after all. Under those circum-
stances you are likely to refrain from generalizing unless there are special
reasons for doing so. Perhaps, for example, you must describe swans to
men who cannot be directly exposed to paradigms. Without superhuman
caution both on your part and on that of your readers, your description
will acquire the force of a generalization; this is often the problem of the
taxonomist. Or perhaps you have discovered some grey birds that look
otherwise like swans but eat different food and have an unfortunate dis-
position. You may then generalize to avoid a behavioural mistake. Or you
may have a more theoretical reason for thinking the generalization worth-
while. For example, you may have observed that the members of other
natural families share colouration. Specifying this fact in a form which
permits the application of powerful logical techniques to what you know
may enable you to learn more about the animal colour in general or about
animal breeding.

Now, having made the generalization, what will you do if you encounter a
black bird that looks otherwise like a swan? Almost the same things, I suggest,
as if you had not previously committed yourself to the generalization at all.
You will examine the bird with care, externally and perhaps internally as
well, to find other characteristics that distinguish this specimen from your
paradigms. That examination will be particularly long and thorough if
you have theoretical reasons for believing that colour characterizes natural
families or if you are deeply ego involved with the generalization. Very
likely the examination will disclose other differentiae, and you will announce
the discovery of a new natural family. Or you may fail to find such differ-
entiae and may then announce that a black swan has been found. Observa-
tion cannot, however, force you to that falsifying conclusion, and you
would occasionally be the loser if it could do so. Theoretical considerations
may suggest that colour alone is sufficient to demarcate a natural family:
the bird is not a swan because it is black. Or you may simply postpone the
issue pending the discovery and examination of other specimens. Only if
you have previously committed yourself to a full definition of ‘swan’, one
which will specify its applicability to every conceivable object, can you be
logically forced to rescind your generalization. And why should you have
offered such a definition? It could serve no cognitive function and would

1 Further evidence for the unnaturalness of any such definition is provided by the follow-
ing question. Should ‘whiteness’ be included as a defining characteristic of swans? If so,
the generalization ‘All swans are white’ is immune to experience. But if ‘whiteness’ is
excluded from the definition, then some other characteristic must be included for which
‘whiteness’ might have substituted. Decisions about which characteristics are to be parts
of a definition and which are to be available for the statement of general laws are often
arbitrary and, in practice, are seldom made. Knowledge is not usually articulated in that
way.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 19

expose you to tremendous risks.! Risks, of course, are often worth taking,
but to say more than one knows solely for the sake of risk is foolhardy.

I suggest that scientific knowledge, though logically more articulate and
far more complex, is of this sort. The books and teachers from whom it is
acquired present concrete examples together with a multitude of theoreti-
cal generalizations. Both are essential carriers of knowledge, and it is there-
fore Pickwickian to seek a methodological criterion that supposes the
scientist can specify in advance whether each imaginable instance fits
or would falsify his theory. The criteria at his disposal, explicit and
implicit, are sufficient to answer that question only for the cases that
clearly do fit or that are clearly irrelevant. These are the cases he expects,
the ones for which his knowledge was designed. Confronted with the
unexpected, he must always do more research in order further to arti-
culate his theory in the area that has just become problematic. He may
then reject it in favour of another and for good reason. But no exclusively
logical criteria can entirely dictate the conclusion he must draw.

Almost everything said so far rings changes on a single theme. The criteria
with which scientists determine the validity of an articulation or an applica-
tion of existing theory are not by themselves sufficient to determine the
choice between competing theories. Sir Karl has erred by transferring
selected characteristics of everyday research to the occasional revolu-
tionary episodes in which scientific advance is most obvious and by there-
after ignoring the everyday enterprise entirely. In particular, he has sought
to solve the problem of theory choice during revolutions by logical criteria
that are applicable in full only when a theory can already be presupposed.
That is the largest part of my thesis in this paper, and it could be the entire
thesis if I were content to leave altogether open the questions that have
been raised. How do the scientists make the choice between competing
theories? How are we to understand the way in which science does
progress?

Let me at once be clear that having opened that Pandora’s box, I shall
close it quickly. There is too much about these questions that I do not
understand and must not pretend to. But I believe I see the directions in
which answers to them must be sought, and I shall conclude with an
attempt briefly to mark the trail. Near its end we shall once more encounter
a set of Sir Karl’s characteristic locutions.

1 This incompleteness of definitions is often called ‘open texture’ or ‘vagueness of
meaning’, but those phrases seem decisively askew. Perhaps the definitions are incomplete,
but nothing is wrong with the meanings. That is the way meanings behave!

20 THOMAS S. KUHN

I must first ask what it is that still requires explanation. Not that scientists
discover the truth about nature, nor that they approach ever closer to the
truth. Unless, as one of my critics suggests,! we simply define the approach
to truth as the result of what scientists do, we cannot recognize progress
towards that goal. Rather we must explain why science—our surest
example of sound knowledge—progresses as it does, and we must first find
out how, in fact, it does progress.

Surprisingly little is yet known about the answer to that descriptive
question, A vast amount of thoughtful empirical investigation is still
required. With the passage of time, scientific theories taken as a group are
obviously more and more articulated. In the process, they are matched to
nature at an increasing number of points and with increasing precision.
Or again, the number of subject matters to which the puzzle-solving
approach can be applied clearly grows with time. There is a continuing
proliferation of scientific specialities, partly by an extension of the bound-
aries of science and partly by the subdivision of existing fields.

Those generalizations are, however, only a beginning. We know, for
example, almost nothing about what a group of scientists will sacrifice in
order to achieve the gains that a new theory invariably offers. My own
impression, though it is no more than that, is that a scientific community
will seldom or never embrace a new theory unless it solves all or almost all
the quantitative, numerical puzzles that have been treated by its pre-
decessor.* They will, on the other hand, occasionally sacrifice explanatory
power, however reluctantly, sometimes leaving previously resolved ques-
tions open and sometimes declaring them altogether unscientific.? Turning
to another area, we know little about historical changes in the unity of the
sciences, Despite occasional spectacular successes, communication across
the boundaries between scientific specialties becomes worse and worse.
Does the number of incompatible viewpoints employed by the increasing
number of communities of specialists grow with time? Unity of the sciences
is clearly a value for scientists, but for what will they give it up? Or again,
though the bulk of scientific knowledge clearly increases with time, what
are we to say about ignorance? The problems solved during the last thirty
years did not exist as open questions a century ago. In any age, the scien-
tific knowledge already at hand virtually exhausts what there is to know,
leaving visible puzzles only at the horizon of existing knowledge. Is it not
possible, or perhaps even likely, that contemporary scientists know less of
what there is to know about their world than the scientists of the eighteenth
century knew of theirs? Scientific theories, it must be remembered, attach

1 Hawkins [1963]. 2 Cf. Kuhn [1958].
3 Cf. Kuhn [1962], pp. 102-8.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 21

to nature only here and there. Are the interstices between those points of
attachment perhaps now larger and more numerous than ever before?

Until we can answer more questions like these, we shall not know quite
what scientific progress is and cannot therefore quite hope to explain it.
On the other hand, answers to those questions will very nearly provide the
explanation sought. The two come almost together. Already it should be
clear that the explanation must, in the final analysis, be psychological or
sociological. It must, that is, be a description of a value system, an
ideology, together with an analysis of the institutions through which that
system is transmitted and enforced. Knowing what scientists value, we
may hope to understand what problems they will undertake and what
choices they will make in particular circumstances of conflict. I doubt
that there is another sort of answer to be found.

What form that answer will take is, of course, another matter. At this
point, too, my sense that I control my subject matter ends. But again, some
sample generalizations will illustrate the sorts of answers which must be
sought. For a scientist, the solution of a difficult conceptual or instru-
mental puzzle is a principal goal. His success in that endeavour is re-
warded through recognition by other members of his professional group
and by them alone. The practical merit of his solution is at best a secondary
value, and the approval of men outside the specialist group is a negative
value or none at all. These values, which do much to dictate the form of
normal science, are also significant at times when a choice must be made
between theories. A man trained as a puzzle-solver will wish to preserve
as many as possible of the prior puzzle-solutions obtained by his group,
and he will also wish to maximize the number of puzzles that can be solved.
But even these values frequently conflict, and there are others which make
the problem of choice still more difficult. It is just in this connection that
a study of what scientists will give up would be most significant. Sim-
plicity, precision, and congruence with the theories used in other specialties
are all significant value for the scientists, but they do not all dictate the
same choice nor will they all be applied in the same way. That being the
case, it is also important that group unanimity be a paramount value,
causing the group to minimize the occasions for conflict and to reunite
quickly about a single set of rules for puzzle solving even at the price of
subdividing the specialty or excluding a formerly productive member."

I do not suggest that these are the right answers to the problem of
scientific progress, but only that they are the types of answers that must be
sought. Can I hope that Sir Karl will join me in this view of the task still
to be done? For some time I have assumed he would not, as a set of phrases

1 Cf. my [1962], pp. 161-9.

22 THOMAS S. KUHN

that recurs in his work seems to bar the position to him. Again and again
he has rejected ‘the psychology of knowledge’ or the ‘subjective’ and in-
sisted that his concern was instead with the ‘objective’ or ‘the logic of
knowledge’.! The title of his most fundamental contribution to our field is
The Logic of Scientific Discovery, and it is there that he most positively
asserts that his concern is with the logical spurs to knowledge rather than
with the psychological drives of individuals. Until very recently I have
supposed that this view of the problem must bar the sort of solution I
have advocated.

But now I am less certain, for there is another aspect of Sir Karl’s work,
not quite compatible with what precedes. When he rejects ‘the psychology
of knowledge’, Sir Karl’s explicit concern is only to deny the methodolo-
gical relevance of an individual’s source of inspiration or of an individual’s
sense of certainty. With that much I cannot disagree. It is, however, a long
step from the rejection of the psychological idiosyncrasies of an individual
to the rejection of the common elements induced by nurture and training
in the psychological make-up of the licensed membership of a scientific
group. One need not be dismissed with the other. And this, too, Sir Karl
seems sometimes to recognize. Though he insists he is writing about the
logic of knowledge, an essential role in his methodology is played by pas-
sages which I can only read as attempts to inculcate moral imperatives in
the membership of the scientific group.

‘Assume’, Sir Karl writes, ‘that we have deliberately made it our task
to live in this unknown world of ours; to adjust ourselves to it as well as we
can;....and to explain it, zf possible (we need not assume that it is) and
as far as possible, with help of laws and explanatory theories. [f we have
made this our task, then there is no more rational procedure than the method
of... conjecture and refutation: of boldly proposing theories; of trying our
best to show that these are erroneous; and of accepting them tentatively if
our critical efforts are unsuccessful.’? We shall not, I suggest, understand
the success of science without understanding the full force of rhetorically
induced and professionally shared imperatives like these. Institutionalized
and articulated further (and also somewhat differently) such maxims and
values may explain the outcome of choices that could not have been
dictated by logic and experiment alone. The fact that passages like these
occupy a prominent place in Sir Karl’s writing is therefore further evi-
dence of the resemblance of our views. That he does not, I think, ever see
them for the social-psychological imperatives that they are is further
evidence of the gestalt switch that still divides us deeply.

1 Popper [1959], pp. 22 and 31 £., 46; and [1963], p. 52.
2 Popper [1963], p. 51. Italics in original.

LOGIC OF DISCOVERY OR PSYCHOLOGY OF RESEARCH? 23

REFERENCES

Braithwaite [1953]: Sccentific Explanation, 1953.

Guerlac [1961]: Lavoisier—The Crucial Year, 1961.

Hafner and Presswood [1965]: ‘Strong Interference and Weak Interactions’, Science, 149,
PP. 503-10.

Hawkins [1963]: Review of Kuhn’s ‘Structure of Scientific Revolutions’, American Journal
of Physics, 31.

Hempel [1965]: Aspects of Scientific Explanation, 1965.

Lakatos [1963-4]: ‘Proofs and Refutations’, The British Journal for the Philosophy of
Science, 14, pp. 1-25, 120-39, 221-43, 296-342.

Kuhn [1958]: ‘The Role of Measurement in the Development of Physical Science’, Isis,
49. pp. 161-93.

Kuhn [1962]: The Structure of Scientific Revolutions, 1962.

Popper [1935]: Logik der Forschung, 1935.

Popper [1945]: The Open Soctety and tts Enemtes, 2 vols, 1945.

Popper [1957]: The Poverty of Historicism, 1957.

Popper [1959]: Logic of Scientific Discovery, 1959.

Popper [1963]: Conjectures and Refutations, 1963.

Stahlman [1956]: ‘Astrology in Colonial America: An Extended Query’, William and
Mary Quarterly, 13, pp. 551-63.

Thorndike [1923-58]: A History of Magic and Experimental Science, 8 vols, 1923-58.

‘Thorndike [1955]: “The True Place of Astrology in the History of Science’, Isis, 46, pp.
273-8.

Against ‘Normal Science’

JOHN WATKINS
London School of Economics

I
A few weeks ago I was asked to reply to Professor Kuhn this afternoon.
Feyerabend and Lakatos were to have given the other papers; but the
first could not come and the second found that, in arranging this collo-
quium, he had brought into existence a many-headed monster attending to
whose multiplying demands would keep him busy approximately twenty-
four hours a day.

This unexpected invitation made me very happy. Kuhn enjoys a unique
position in the English speaking world as a philosophically-minded his-
torian and historically-minded philosopher of science. I felt that it would
be a privilege and a pleasure to reply to his paper.

For Kuhn, however, the programme change was not so agreeable. He
had expected that Feyerabend and Lakatos would write independent
papers so that his own would not need to be ready until this afternoon.
Now he found that I was to reply to his paper, which rather suggested that
I should see it beforehand. He responded herioically, rushing bits of his
paper across the Atlantic as they left his typewriter. During much of last
week I felt like a reader of a cliff-hanging serial, eagerly awaiting the next
instalment. Thus my own paper has been written in a rush; and this has, I
fear, aggravated my tendency to wave aside details and qualifications in
trying to come to grips with someone’s ideas.

In the turmoil of the last few days I have had one great stand-by.
Kuhn’s book, The Structure of Scientific Revolutions, isa famous book and
one with which I am tolerably well acquainted. I was privileged to read it
in manuscript in 1961 and to discuss it with its author. In 1963 it was dis-
cussed at length at Sir Karl Popper’s seminar, where Mr Hattiangadi gave
a paper on it (which he afterwards expanded into a very interesting disserta-
tion), Later, I shall quote something which Popper said then; and I
expect that my paper will contain some unconscious borrowings from our
Seminar discussions.

So my paper will be as much about Kuhn’s book as about the paper he
has just read. Fortunately, this is appropriate, since in his paper Kuhn
has adopted a Sukarno-like policy of confrontation between the view of
Science propounded in his book, and Popper’s view of science. I am glad

2 25

26 JOHN WATKINS

that he has done this. I remember suggesting to him in 1961 that he should
bring out and discuss in his book the clash between his view of the
scientific community as an essentially closed society, intermittently
shaken by collective nervous breakdowns followed by restored mental
unison, and Popper’s view that the scientific community ought to be, and
to a considerable degree actually is, an open society in which no theory,
however dominant and successful, no ‘paradigm’ to use Kuhn’s term, is
ever sacred. Kuhn did not follow this suggestion at the time, but he has
surely made the amende honorable this afternoon.

Yet two things leave me a little discontented with the way in which he
has arranged the confrontation. For one thing, as presented by him, it is
by no means as dramatic as it might be. Near the beginning he says: ‘On
almost all the occasions when we turn explicitly to the same problems, Sir
Karl’s view of science and my own are very nearly identical’. My aim will
be to bring out the larger conflicts between these two views. At this stage I
will just cite one remark in Kuhn’s paper which, as it were, incapsulates the
main conflict in a sentence: ‘it is precisely the abandonment of critical
discourse that marks the transition to a science.”

The second source of my discontent is different. A Sukarno-style con-
frontation involves, not only a major ideological clash, but also a good deal
of local skirmishing. I hope Kuhn will forgive me if I confine most of my
counter-skirmishing to a footnote.? In my text I shall concentrate upon his
idea—it is an original and challenging idea—of Normal Science. There
will be a certain conscious unfairness, or at least one-sidedness, in my dis-

1 This volume, p. 1.

2 This volume, p. 6.

3 Kuhn’s method is to pick out a few ‘characteristic locutions’, and to erect on these some
construction at which he can nag away. But his constructions sometimes bear a rather
faint resemblance to what was said in the books from which the locutions were picked.
(Kuhn himself sometimes admits that a construction of his does not quite fit. Thus on
p. 14 he writes: ‘Though he is not a naive falsificationist, Sir Karl may, I suggest, legiti-
mately be treated as one.’) For instance, Kuhn ponders with much head-shaking the
‘locution’ that ‘we can learn from our mistakes’. He seems unable to allow that Popper
was using the word ‘mistake’ in a cheerfully guilt-free sense with no suggestion of personal
failure, rule-transgression, etc. The physicist J. E. Wheeler was using the word in a Popperian
spirit when he wrote: ‘Our whole problem is to make the mistakes as fast as possible’
(Wheeler [1956], p. 360).

Since Kuhn’s main target was Popper’s demarcation criterion, and since Popper has
stated this pretty sharply, one might have expected that here, at least, Kuhn would have
given chapter and verse. But no, he prefers once more to moot a construction of his own:
‘Demarcation might . . . be achieved by an exclusively syntactic criterion. Sir Karl’s view
would then be, and perhaps is, that a theory is scientific if and only if observation statements
—-particularly the negations of singular existential statements—can be logically deduced
from it...’ (p. 14). If one consults Popper’s [1934], section 21, one finds that this is full
of mistakes (in Kuhn’s sense).

AGAINST ‘NORMAL SCIENCE’ 27

cussion of this idea. I believe that it is of considerable sociological import-
ance. A sociologist investigating the scientific profession as he might in-
vestigate, say, the medical profession, might do well to use it as his ideal
type. But I shall consider it from a methodological point of view, and
methodology, as I understand it, is concerned with science at its best, or
with science as it should be conducted, rather than with hack science.

My programme will be this. I shall begin, in section II, by confronting
Kuhn’s account of Normal Science with the sort of appraisal which Popper
would make of a scientific situation which lived up to—or down to—
Kuhn’s idea of Normal Science. Then, in section III, I shall ask why
Kuhn should claim that Normal Science, as opposed to what he -calls
Extraordinary Science, constitutes the essence of science. Lastly, in section
IV, I shall ask whether Normal Science could be as Kuhn describes it and
yet give rise to Extraordinary Science. My answer will be, ‘No’; and I will
suggest that this answer happily rebuts Kuhn’s view of scientific nor-
malcy as a closed society of closed minds.

In considering Kuhn’s idea of Normal Science from a Popperian point of
view, it is natural that I should concentrate upon what Kuhn says about
testing within Normal Science. Tests, he says, are being conducted all the
time, but ‘these tests are of a peculiar sort, for in the final analysis it is
the individual scientist rather than current theory which is tested’.! His
idea is this. So-called ‘testing’ in Normal Science is not testing of theories.
Rather, it is part of puzzle-solving activity. Normal Science is governed by
some paradigm (or dominant theory). The paradigm is trusted implicitly;
but it will not fit experimental findings quite perfectly. There will always
be apparent discrepancies or anomalies. Normal Research largely consists
of resolving these anomalies by making suitable adjustments which leave
the paradigm intact. The paradigm is taken as guaranteeing the existence
of a solution to every puzzle generated by apparent discrepancies between
it and observations. Hence, although the ‘tests’ carried out within Normal
Science may /ook like tests of the prevailing theory if viewed through
Popperian spectacles, they are really tests of something else, namely the
experimenter’s puzzle-solving skill. If the outcome of such a ‘test’ is
negative, it does not hit the theory but backfires on the experimenter. His
prestige may be lowered by the failure of his attempt to solve a puzzle;
but the prestige of the paradigm within whose framework he makes the
attempt is so high that it will scarcely be affected by any such little local
difficulties.

1 This volume, p. 5.

28 JOHN WATKINS

[ According to Kuhn it is only at a time of what he calls Extraordinary
Science, when the prevailing theory itself is under attack, that something
jike genuine testing of theories may occur. Then a negative outcome of a
test may be regarded, not as the personal failure of the experimenter, but as
a failure of the theory. In Kuhn’s words, ‘A failure that had previously been
personal may then come to seem the failure of a theory under test’.1

For Kuhn, Normal Science is, as the name suggests, the normal con-
dition of science; Extraordinary Science is an abnormal condition; and
within Normal Science, to repeat, the genuine testing of prevailing theories
is rendered, in some rather mysterious psychological-cum-sociological
way, impossible. (One can now see how Kuhn could be startled by a
remark which he at the same time regards as ‘virtually a clichée’,? namely,
Popper’s remark that scientists put forwards statements and test them step
by step. For Kuhn it zs virtually a cliché to say that scientists normally
engage in a lot of testing: they test their solutions to anomaly-generated
puzzles; and it is, for him, startlingly incorrect to say that it is normal for
scientists to test theories.)

That it is desirable that a theory should be defended with a certain dog-
matism, so that it is not knocked out too quickly before its resources have
been explored, Popper has never denied; but such dogmatism is healthy
only so long as there are other people around who are not inhibited from
criticizing and testing a tenaciously defended theory. If everyone were
under some mysterious compulsion to preserve the current theories of
science against awkward results, then those theories would, according to
Popper, lose their scientific status and degenerate into something like
metaphysical doctrines. ;

Thus we have the following clash: the condition which Kuhn regards as
the normal and proper condition of science is a condition which, if it
actually obtained, Popper would regard as unscientific, a state of affairs in
which critical science had contracted into defensive metaphysics. Popper
has suggested that the motto of science should be: Revolution in permanence!
For Kuhn, it seems, a more appropriate maxim would be: Not nostrums but
normalcy!

In his paper today Kuhn spoke of Popper’s emphasis on the asymmetry
between the falsifiability and the non-verifiability of scientific generaliza-
tions as ‘a forward step from which there must be no retreat’.3 He added
that the ‘same asymmetry plays a fundamental role in my Structure of
Scientific Revolutions ...1 may well have taken it from what I had heard
of his work.’ But Kuhn’s memory seems to have played a trick on him

1 This volume, p. 7. ® This volume, p. 4.
3 This volume, p. 13-

AGAINST ‘NORMAL SCIENCE’ 29

here: in his book he had referred explicitly to Popper’s thesis that there is
no verification and that falsification is what matters,! and he did so in order
to dismiss that thesis as unrealistic, on the ground that in Normal Science
there is no falsification of theories, while in Extraordinary Science the
evidence which is taken as falsifying the paradigm which is being ushered
out will also be taken as verifying the new paradigm which is being ushered
in.?

In his Structure of Scientific Revolutions Kuhn did not advance any
demarcation-criterion for science; he only set aside Popper’s falsifia-
bility-criterion. Now he advances an alternative criterion of his own:
Finally, and this is for now my main point, a careful look at the scientific enterprise
suggests that it is normal science, in which Sir Karl’s sort of testing does not occur,
rather than extraordinary science which most nearly distinguishes science from
other enterprises. If a demarcation criterion exists (we must not, I think seek a
sharp or decisive one), it may lie just in that part of science which Sir Karl ignores.*

That was cautiously worded. But on the next page Kuhn was bolder:
‘of the two criteria, testing and puzzle-solving, the latter is at once the less
equivocal and the more fundamental’.t And I will throw any remaining
caution of Kuhn’s to the winds and re-state his suggestion in an unguarded
way: Normal Science (in which there is not really any testing of theories),
is genuine science; Extraordinary Science (in which genuine testing of
theories does occur) is so abnormal, so different from genuine science,
that it can hardly be called science at all. Kuhn explains that it is because
puzzle-solving is easily mistaken for testing that ‘Sir Karl’s line of demarca-
tion and my own so frequently coincide’.® Well, the ines may coincide;
but they divide the material in opposite ways. What is genuinely scientific
for Kuhn is hardly science for Popper, and what is genuinely scientific for
Popper is hardly science for Kuhn.

Kuhn advances the following consideration against Popper’s criterion
and in favour of his own: it has often happened in the history of science
that a theory was replaced before it had failed a test but not ‘before it had
ceased adequately to support a puzzle-solving tradition’®; hence testing is
not, after all,so very important: “To rely on testing as the mark of a science
is to miss what scientists mostly do and, with it, the most characteristic
feature of their enterprise.’?

But first, what Popper relies on as the mark of a scientific theory is not
that it has actually been tested but that it is testable, the more testable the

1 Kuhn [1962], p. 145.

2 ‘But falsification, though it surely occurs, .. . might equally well be called verification
since it consists in the triumph of a new paradigm over the old one’ (Kuhn [1962], p. 146).

3 This volume, p. 6. 4 This volume, p. 7. 5 This volume, p. 7.
® This volume, p- 10. 7 This volume, p. 10.

30 JOHN WATKINS

better (other things being equal). So it is entirely in line with his phil-
osophy of science that one scientific theory should be replaced by a more
testable theory even though the previous theory has not yet failed a test.

Second, by contrast with the relatively sharp idea of testability, the
notion of ceasing ‘adequately to support a puzzle-solving tradition’ is
essentially vague; for since Kuhn insists that there are always anomalies
and unsolved puzzles,! the difference between supporting, and failing to
support, a puzzle-solving tradition is merely one of degree: there must be a
critical level at which a tolerable turns into an intolerable amount of
anomaly. Since we do not know what the critical level is, this is the sort of
criterion that can be used only retrospectively: it entitles us to declare,
after a paradigm-switch has occurred, that empirical pressure on the old
paradigm must have become pretty intolerable. (This fits in well with
Kuhn’s idea that a reigning paradigm has such a sway over men’s minds
that only strong empirical pressure can dislodge it.)

But the history of science contains important examples of an empirically
successful dominant theory being superseded by an incompatible and more
testable theory. Let me mention one such example. Before Newton, Kepler’s
laws constituted the dominant theory of the solar system. I take it that it is
no longer necessary to argue that Newtonian theory is strictly incompatible
with Kepler’s original laws—if we speak of the latter being incorporated in,
or subsumed under, the former, then we should add that it is significantly
modified versions of those laws that follow from Newton’s theory.’ If
Kuhn allows that Kepler’s theory was a paradigm and that it was incom-
patible with the Newtonian paradigm, then he must, I think, allow that
this was a case of paradigm-change. So the question arises: is it plausible
to maintain that the Keplerian paradigm ‘had ceased adequately to support
a puzzle-solving tradition’?

Well, there was, prior to Newton, an unsolved puzzle connected with
Kepler’s laws. Newton himself mentions ‘a perturbation of the orbit of
Saturn in every conjunction of this planet with Jupiter, so sensible, that
astronomers are puzzled with it.’* But since, for Kuhn, there are always
unsolved puzzles, this can hardly amount to failure ‘to support a puzzle-

1 Kuhn [1962], p. 81.

® Over fifty years ago Pierre Duhem wrote: ‘The principle of universal gravity, very far
from being derivable by generalization and induction from the observational laws of Kepler,
formaily contradicts these laws. If Newton’s theory is correct, Kepler’s laws are necessarily
false’ (Duhem [1914], p. 193 of the 1954 English translation). For a more detailed analysis
of inconsistencies between Newtonian theory and Kepler’s laws—inconsistencies which
mean that the latter have first to be corrected in important ways before they can be explained
by the former—see Popper [1957] and [1963], p. 62 n.

8 Newton [1687], discussion to Book III, Prop. xiii. Professor J. Agassi drew my atten-
tion to this passage. (He discusses it in his [1963], p. 79, footnote 5.)

AGAINST ‘NORMAL SCIENCE’ 31

solving tradition’. Newton, at any rate, seems to have been far from re-
garding the Keplerian system as having failed in any way. In the Proposi-
tion to which the above-quoted remark is annexed, he stated Kepler’s first
two laws in an uncorrected form,! thereby helping to initiate the legend
perpetuated by Halley who, in his review of the Principia, wrote, ‘Here
[in Book III] the verity of the Hypothesis of Kepler is demonstrated.”

It seems that a dominant theory may come to be replaced, not because of
growing empirical pressure (of which there may be little), but because a
new and incompatible theory (inspired perhaps by a different metaphys-
ical outlook) has been freely elaborated: a scientific crisis may have theo-
retical rather than empirical causes.3 If that is so, there is more free think-
ing in science than Kuhn supposes. I will revert to this issue in the last
section.

Later, I shall argue that Normal Science cannot have the character Kuhn
ascribes to it, if it is to be capable of giving rise to Extraordinary (or Revo-
lutionary) Science. But for the time being I shall suppose that the history
of science does indeed display a Kuhnian pattern; that is, I shall suppose
that a typical cycle consists of a longish period of Normal Science, which
gives way to a short and hectic bout of Extraordinary Science, after which
a new period of Normal Science sets in.

The question I now ask is, Why is Kuhn concerned to up-value Normal
Science and down-value Extraordinary Science? This question is prompted
by several considerations. First, Normal Science seems to me to be rather
boring and unheroic compared with Extraordinary Science. Kuhn himself
thinks it a mistake, but a rather natural mistake, to regard Normal Science
as ‘an intrinsically uninteresting enterprise’,* and he agrees that Normal
Science is comparatively unproductive of new ideas. More accurate deter-
minations of physical constants—that is the sort of thing achieved by the
‘mopping-up operations’ which constitute Normal Science.> Second,
Kuhn has re-iterated this afternoon that he, like Popper, rejects ‘the view
that science progresses by accretion’®; but if he were asked in what manner
Normal Science progresses, he would, presumably, say that it does so in

1 Newton [1687], Book III, Prop. xiii. As to Kepler’s third law, see Book I, Prop. iv,
cor. vi., and also Newton (1669].

2 Halley [1687], p. 410.

3 The nearest Kuhn approaches this is in his admission that a new paradigm may emerge,
‘at least in embryo, before a crisis has developed far’ (Kuhn [1962], p. 86, my italics).
That it might emerge before a crisis has developed at al/, and might itself generate a crisis,
is excluded by his idea of paradigm-dominance within Normal Science.

4 This volume, p. 6. ‘ 5 Kuhn [1962], pp. 24 and 27.

& This volume, p. 1.

32 JOHN WATKINS

an orderly, undramatic, step by step manner, i.e. it progresses by accre-
tion. Why has Kuhn, despite his concern ‘with the dynamic process by
which scientific knowledge is acquired’, come to identify science with its
periods of theoretical stagnation? Third, why has the author of one excel-
lent book on the Copernican revolution, and of another more famous
book on scientific revolutions generally, taken a sort of philosophical dislike
to scientific revolutions? Why is he so enamoured with plodding, uncritical,
Normal Science?

One answer, though I suspect that it is not the main answer, is that he
has been impressed by sheer quantitative considerations: there is much
more Normal Science, measured in man-hours, than Extraordinary
Science. Normal Science, Kuhn says, ‘accounts for the overwhelming
majority of the work done in basic science’.? The sort of scientific develop-
ments with which Popper is concerned are ‘very rare’.

From a sociological point of view it may be quite in order to discount
something on the ground that is rare. But from a methodological point of
view, something rare in science—a path-breaking new idea or a crucial
experiment between two major theories—may be far more important than
something going on all the time.

But I do not think that these quantitative considerations were decisive
for Kuhn. I suspect that a very different sort of consideration was at work.
As this matter is a little personal and delicate, and as my evidence is all
drawn from Kuhn’s book, I will not blurt out my conjecture straightaway,
but will lead up to it gradually. I will start by considering how far Kuhn’s
demarcation-criterion succeeds in excluding certain intellectual disciplines
that few of us would want to call scientific.

It is interesting that Kuhn himself should have mentioned, in this con-
nection, that he does not ‘want to join Sir Karl in labelling astrology a
metaphysic rather than a science’.4 One can see why: the careful drawing
up of a horoscope, or of an astrological calendar, fits Kuhn’s idea of
Normal Research rather nicely. The work is done under the aegis of a

1 This volume, p. 1, my italics.

2 This volume, p. 4.

3 This volume, p. 5.

4 This quotation is from the original draft of Kuhn’s paper. He now says that ‘Sir Karl
is right to exclude astrology from the sciences’ (p. 10, my italics)—right, but for the wrong
reasons: for there were predictive failures in astrology (though these could always be
‘explained’); on the other hand, astrologers ‘had no puzzles to solve and therefore no
science to practise’ (p. 9).

This new revelation of the subtlety of Kuhn’s puzzle-concept leaves me boggling. I
knew that a predictive failure may be regarded as a mere puzzling anomaly, and that it may
later, when the framework changes, come to be regarded as a refutation. I had not appreci-
ated that there can be predictive failures which are regarded neither as refutations nor as
posing any puzzle.

AGAINST ‘NORMAL SCIENCE’ 33

stable body of doctrine which is not discredited, in the eyes of astrologers,
by predictive failures.

More interesting, apropos Kuhn’s possible reasons for depreciating
revolutionary science, is another sort of case which seems to fit his idea of
Normal Research all too well. Consider a theological scholar working on
an apparent inconsistency between two Biblical passages. Theological doc-
trine assures him that the Bible, properly understood, contains no incon-
sistencies. His task is to provide a gloss that offers a convincing reconcilia-
tion of the two passages. Such work seems essentially analogous to ‘normal’
scientific research as depicted by Kuhn; and there are grounds for sup-
posing that he would not repudiate the analogy. For The Structure of
Scientific Revolutions contains many suggestions, some explicit, others
implicit in the choice of language, of a significant parallelism between
science, especially Normal Science, and theology. Kuhn writes of a
scientific education as a ‘process of professional initiation’! which ‘prepares
the student for membership in the particular scientific community’.? He
says that ‘it is a narrow and rigid education, probably more so than any
other except perhaps in orthodox theology’? He also says that a scientific
education involves the re-writing, in text-books, of history backwards, and
that this indicates ‘one of the aspects of scientific work that most clearly
distinguishes it from every other creative pursuit except perhaps theology’ 4
In other places the suggestion of a science-theology parallelism, though
less explicit, is no less obvious. For example, he says that Normal Science
‘often suppresses fundamental novelties because they are necessarily sub-
versive of its basic commitments.’ And when Kuhn discusses the personal
process of repudiating an old paradigm and embracing a new one, he
describes it as a ‘conversion experience’,® adding that ‘a decision of that
kind can only be made on faith.””

My suggestion is, then, that Kuhn sees the scientific community on the
analogy of a religious community and sees science as the scientist’s religion.
If that is so, one can perhaps see why he elevates Normal Science above
Extraordinary Science; for Extraordinary Science corresponds, on the
religious side, to a period of crisis and schism, confusion and despair, to a
spiritual catastrophe.

IV
Hitherto, I have been considering Kuhn’s comparative evaluations of
Normal and Extraordinary Science on the supposition that the history of

1 Kuhn [1962], p. 47. 2 Op. cit. p. 11.

3 Op. cit., p. 165, my italics. 4 Op. cit. p. 135, my italics.
5 Op. cit. p. 5. 8 Op. cit. p. 150,

7 Op, cit. p. 157

34 JOHN WATKINS

science does in fact display a Normal Science/Extraordinary Science/
Normal Science cycle. I shall now challenge this supposition.

One way of challenging it would be to point to historical counter-
examples, that is, to long stretches of scientific history in which no chear
paradigm emerged and during which the typical symptoms of Normal
Science were absent. I remember Popper saying (in the course of our
seminar discussion of Kuhn’s book) that, although Newtonianism did
turn into something like a paradigm in Kuhn’s sense, no such paradigm
emerged during the long history of the theory of matter!: here from the pre-
Socratics to the present day there has been an unending debate between
discontinuous and continuous concepts of matter, between various atomic
theories on the one hand, and ether, wave and field theories on the other.

I wish to raise a different objection. My objection concerns the possi-
bility of the emergence of a new paradigm at the end of a period of Normal
Science. I shall not criticize the epidemiological account he gave in his
book of how, after a new paradigm has infected a few carriers, the epidemic
is liable to spread among the scientific community. In what follows I shall
focus attention on the very first scientist to take up a new paradigm. My
thesis will be that a new paradigm never could emerge from Normal
Science as characterized by Kuhn.

I begin by recapitulating some Kuhnian theses concerning paradigm
change.

(1) It is in the nature of a paradigm to enjoy a monopoly in its hold on a
scientist’s thinking. A paradigm brooks no rivals: it is built into Kuhn’s
concept of a paradigm that one scientist cannot, while under the sway of
one paradigm, seriously entertain a rival paradigm. If he has started toying
with a rival paradigm, then the old paradigm is already defunct for him. I
call this the Paradigm-Monopoly thesis.

(2) There is little or no interregnum between the end of the old para-
digm’s reign over ascientist’s mind, and the beginning of the new paradigm’s
reign. A scientist does not flounder around for any substantial length of

time with no paradigm to guide him. He abandons one paradigm only to .

embrace a new one. (It is as if his cry were, The Paradigm 1s dead. Long live
the Paradigm.) { call this the No-Interregnum thesis.

(3) A new paradigm will be incompatible with the paradigm it super-
sedes.? (Indeed, Kuhn goes further and claims that the new paradigm will
be incommensurable with the old one.* I will discuss the relation between
incompatability and incommensurability later.) I call Kuhn’s thesis con-
cerning the clash between old and new paradigms the Incompatibility

1 A similar point has been made independently by Dudley Shapere: cf. his [1964], p. 387.
2 Kuhn [1962], pp. 91 and 102. 3 Op cit. pp. 4, 102, 111 and 147

AGAINST ‘NORMAL SCIENCE’ 35

thesis. (This thesis obviously re-inforces the Paradigm-Monopoly
thesis.)

(4) From the conjunction of the above three theses it follows that a
scientist’s change-over from an old paradigm to a new one must be pretty
swift and decisive. Kuhn emphatically endorses this implication. We have
already noticed him referring to a paradigm-switch as a ‘conversion’; and
from other passages in his book it is clear that he holds that such conver-
sions are quick. He says that a paradigm-switch is ‘a relatively sudden and
unstructured event like the gestalt switch’,! and that ‘the transition
between competing paradigms cannot be made a step at a time . . . Like the
gestalt switch, it must occur all at once (though not necessarily in an
instant)’.? I call this the Gestalt-Switch thesis.

(5) I now consider the implications of the fore-going theses for the
invention of a new paradigm. Kuhn’s view allows that it may take quite a
time for a paradigm, once invented, to gain general acceptance. The ques-
tion now is: how long may it take the original inventor to put together the
rudiments of the new paradigm? To put it another way: what sort of pre-
history could his new paradigm have? The answer implied the Gestalt-
Switch thesis appears to be: none at all. Before he switched over to it his
thinking was along irreconcilably different lines (by the Paradigm-Mono-
poly and Incompatibility theses). His switch to the new paradigm must be
regarded as the very same thing as his invention of the new paradigm. (I am
assuming that it was invented inside the scientific community and not
imported from extra-scientific sources.) And since the switch to it was
‘relatively sudden’ the invention of it must have been relatively sudden,
too. Kuhn endorses this implication. In his book he wrote: “The new
paradigm, or a sufficient hint to permit later articulation, emerges all at
once, sometimes in the middle of the night, in the mind of a man deeply
immersed in crisis’.* And this afternoon he repeated that theories are
‘invented in one piece’.* I call this, a shade maliciously, the Instant-
Paradigm thesis. (Instant coffee takes more than an instant to make; but
it is made ‘all at once’, unlike steak-and-kidney pie, which might be said
to ‘be made a step at a time’.)

We must remember that the new paradigm is immediately powerful
enough to induce our scientist to turn against the well-articulated and
unrefuted paradigm that has dominated his scientific thinking hitherto.
This means, I take it, that the new paradigm cannot begin as just a few
fragmentary ideas, but must at the outset be large and definite enough for
its striking potentialities to be fairly apparent to its inventor.

2 Op. cit. p. 149.
4 This volume, p. 12.

1 Op cit, p. 121.
2 Op cit. p. 89.

36 JOHN WATKINS

If that is so, the Instant-Paradigm thesis seems to me to be barely
credible on pyschological grounds. I do not know how much a single genius
might achieve in the middle of the night, but I suspect that this thesis
expects too much of him. In any case, there are, surely historical counter-
examples to it. To mention one: the Inverse Square Law was an important
component of Newtonian theory (which Kuhn regards as a paradigm of
paradigms); and Pierre Duhem has traced the long evolution of the
Inverse Square Law back through Hooke, Kepler, and Copernicus, to
Aristotle’s idea that bodies seek the centre of the earth. I conclude that the
Instant-Paradigm thesis must be rejected.

The Instant-Paradigm thesis followed from the Gestalt-Switch thesis
when the latter was applied to the first man to switch over. And the
Gestalt-Switch thesis followed from the conjunction of the Paradigm-
Monopoly, No-Interregnum, and Incompatibility theses. Hence at least
one of these three theses must be rejected if the Instant-Paradigm thesis
is rejected. I will consider the Incompatability thesis first.

There seems to be a certain internal incoherence in Kuhn’s version of
this thesis. He says that what ‘emerges from a scientific revolution is not
only incompatible but often actually incommensurable with what has gone
before’.2 But could two incommensurable theories be logically incompatible
with each other? If someone holds that, say, Biblical myths and scientific
theories are incommensurable, belong to different universes of discourse,
he presumably implies that the Genesis account of the Creation should not
be regarded as logically incompatible with geology, Darwinism, etc.: they
are compatible and can peacefully co-exist just because they are incom-
mensurable. But if the Ptolemaic system is logically incompatible with the
Copernican system, or Newtonian theory with Relativity theory, peaceful
co-existence is not possible: they were rival alternatives; and it was
possible to make a rational choice between them partly because it was
possible to devise crucial experiments between them (stellar parallax, star-
shift, etc.).

So let us disengage Kuhn’s Incompatibility thesis from the alien idea of
incommensurability. Thus purified, this historical thesis of Kuhn’s is in
happy accord with a methodological thesis of Popper’s. For if the new
theory is to be highly testable, as Popper’s methodology demands, it

1 Duhem, op. cit. chapter vii, section 2. Duhem himself gave this example in support of
his emphatically negative answer ‘Surely no’ to the question: ‘Is [a man’s] mind powerful
enough to create a physical theory all out of one piece?’ (op. cit. chapter vii, section 2).
Agassi has labelled Duhem’s own view of the evolution of scientific ideas ‘the continuity
theory’ (Agassi [1963], pp. 31 ff.). Agassi attacks the historiographical method sponsored
by this view; he does not, of course, advance the counter-claim that theories are invented
in one piece. ? Kuhn [1962], p. 102.

AGAINST ‘NORMAL SCIENCE’ 37

should yield (not only some remarkable predictions beyond the predictive
scope of existing theories, but) some predictions which conflict with those
of existing theories, preferably in areas where the existing theories have
been well tested and have not, so far, been faulted. Popper says, in effect,
that major theoretical advances in science ought to have a revolutionary
character; and Kuhn says, in effect, that they do have a revolutionary
character. Good. Let us agree that the Incompatibility thesis should stay.

Then the Paradigm-Monopoly thesis and/or the No-Interregnum thesis
must go. But these really hang together. The second says that a scientist’s
professional thinking is always paradigm-dominated, the first says that it
is, at any one time, dominated by one paradigm. Against this I have main-
tained that since it takes time—a matter of years rather than of hours—-to
develop a potential new paradigm to the point where it may challenge
an entrenched paradigm, heretical thinking must have been going on for a
long time before paradigm-change can occur. This means that it is not
true that a reigning paradigm exercises such a monopolizing sway over
scientists’ minds that they are all unable to consider it critically, or to toy
with (without necessarily embracing) alternatives to it. It means that the
scientific community is not, after all, a closed society whose chief character-
istic is ‘the abandonment of critical discourse’,

REFERENCES

Agassi [1963]: Towards an Historiography of Science, 1963.

Duhem [1914]: La théorie Physique: son Objet et sa Structure, 1914.

Halley [1687]: Review of Newton’s Principia, Philosophical Transactions, 1687, Reprinted
in I, B. Cohen (ed.): Isaac Newton’s Papers and Letters on Natural Philosophy, 1958,
PP. 405-11.

Kuhn [1962]: The Structure of Scientific Revolutions, 1962.

Newton [1669]: Manuscript, reprinted in Turnbull (ed.): The Correspondence of Isaac
Newton, Ip pp. 297-303.

Newton [1687]: Philosophiae Naturalis Principia Mathematica, 1687.

Popper [1934]: Logik der Forschung, 1935.

Popper [1957]: ‘The Aim of Science’, Ratio, 1, pp. 24-35.

Popper [1963]: Conjectures and Refutations, 1963.

Shapere [1964]: “The Structure of Scientific Revolutions’, The Philosophical Review, 73,
Pp. 383-94.

Wheeler [1956]: ‘A Septet of Sibyls: Aids in the Search for Truth’, The American Scientist,
44, pp. 360-77.

Does the Distinction between Normal and
Revolutionary Science Hold Water?

STEPHEN TOULMIN
University of Michigan

Professor T. S. Kuhn’s contribution to this Symposium can be looked at
from two angles: either as a critique of Sir Karl Popper’s approach towards
the philosophy of science, in the light of its contrasts with Professor Kuhn’s
own views, or alternatively, as a further instalment in the development of
Kuhn’s analysis of the process of scientific change. My concern here is
with the second of these two aspects. I shall draw attention to certain
significant changes in the position Kuhn now appears to be occupying
from those which he adopted, first in his original paper on “The Function
of Dogma in Scientific Research’ read at Worcester College, Oxford, in
1961,/ and subsequently in his book The Structure of Scientific Revolutions
published in 1962. And in the light of changes, I shall suggest how we might
see our way beyond Kuhn’s theory of ‘scientific revolution’ to a more
adequate theory of scientific change.

The great merit of Professor Kuhn’s insistence on the ‘revolutionary’
character of some changes in scientific theory is that it has compelled many
people to face for the first time the full profundity of the conceptual
transformations which have, at times, marked the historical development of
scientific ideas. Yet from the beginning it was clear to many onlookers that
Kuhn’s original statement of his position was, in at least two respects, only
provisional. Some of us have been waiting with interest to see in what
direction his own intellectual development took him next. In the first
place, although his choice of the word ‘dogma’ served well enough in the
title of a thought-provoking paper at the Worcester College meeting, only a
little closer examination was required to reveal the fact that its very effect-
iveness sprang from a certain built-in rhetorical exaggeration or play upon
words. (To say ‘all normal science rests on a foundation of dogma’ was like
saying ‘we are all mad really’; which can make a point on a particular
occasion, but. . .)

The nature of this play upon words becomes evident if we contrast the
application of Kuhn’s analysis to Newton’s Principia, regarded as the
founding document of classical mechanics, with its application to Newton’s
Opticks, which was so influential in eighteenth-century physics. Taking

1 Printed in Crombie (ed), [1963], pp. 347-69.

40 STEPHEN TOULMIN

Principia first, we can state a worthwhile philosophical point as follows:
that the intellectual function of an established conceptual scheme is to
determine the patterns of theory, the meaningful questions, the legitimate
interpretations, etc., within which theoretical speculation is bounded for
as long as that particular conceptual scheme retains intellectual authority
within the natural science concerned. This (I repeat) is a philosophical
point, which indicates something of what is involved in saying that scien-
tific procedures, in the theoretical as well as the practical area, are ‘meth-
odical’, and marked by plain good sense. However, this particular point
does nothing at all to establish that dogma has any part to play in scientific
theory. On the contrary, it was wholly reasonable—and undogmatic—for
physicists between 1700 and 1880 to accept Newton’s dynamics as their
provisional starting-point. And it is always open to scientists to challenge
the intellectual authority of the fundamental scheme of concepts within
which they are provisionally working—the permanent right to challenge
this authority being one of the things which (as Sir Karl Popper has always
insisted) marks off an intellectual procedure as being ‘scientific’ at all.
Incidentally, this first, philosophical point was stated rather more clearly
and unambiguously, some twenty-five years ago, by R. G. Collingwood in
his Essay on Metaphysics: The intellectual function of Kuhn’s ‘paradigms’
is precisely that of Collingwood’s ‘absolute presuppositions’.

Alternatively, if we take Newton’s Opticks as our example, we may make
a sociological point, as follows: that there is a tendency on the part of
secondary workers in science to see only part of the intellectual picture in
the subject with which they are concerned, and to restrict the choice of
hypotheses by which they interpret their data, out of deference to the
supposed example set them by a primary worker, whom they take as their
master and whose magisterial authority they bow to. This is a sociological
rather than a philosophical point: in this case, one can indeed speak of
‘dogma’ playing a part in the development of scientific ideas. But the very
beginning of wisdom in any attempt to understand the nature of intellec-
tual development in science must, surely, be to distinguish between the
intellectual authority of an established conceptual scheme and the magis-
terial authority of a dominant individual. And it is only when secondary
workers insist on retaining, say, a corpuscularian theory of light out of
respect for the authority of Newton, even after legitimate alternatives have
been put forward with as much experimental support, that the word
‘dogma’ has any relevance to science.

Kuhn, in moving on from his Oxford paper to the 1962 book, withdrew

1 Collingwood [1940], esp. chapters iv—vi. Collingwood’s argument is discussed, in
parallel with Kuhn’s, in my [1966].

DISTINCTION BETWEEN NORMAL AND REVOLUTIONARY SCIENCE 41

his insistence on the term ‘dogma’, but attempted to retain a central
distinction between ‘normal science’ and ‘scientific revolutions’. Through-
out the book he regarded the idea of ‘revolutions’ as having some power to
illuminate and explain certain phases in scientific change. In this respect,
too, his analysis was at best only provisional. As we know from political
history, the term ‘revolution’ may serve as a useful descriptive label, but it
has long since worn out its value as an explanatory concept. At one time,
historians faced with political changes of a peculiarly drastic variety were
quite ready to say, ‘...and then there was a revolution’, and leave it at
that: the implication was that, in the case of such drastic changes, no
explanation could be given of the rational kind we rightly demand in the
case of normal political developments. But in due course they were com-
pelled to recognize that political change never in fact involves such an
absolute and outright breach of continuity. Whether one considers the
French Revolution, the American Revolution or the Russian Revolution, in
each case the continuities in political and administrative structure and
practice are quite as important as the changes. (Consider, for instance, the
American legal system, the Russian practice of escorting tourists, and the
French code of inheritance: the effect of political revolution was to change
each of these only marginally, and the corresponding states of affairs in
each country before and after the revolution in question were much more
similar than the pre-revolutionary or post-revolutionary conditions in the
different countries.) So, in the political sphere, statements about the occur-
rence of ‘revolutions’ are only preliminary to questions about the political
mechanisms involved in revolutionary change. As the explanatory level,
the difference between normal and revolutionary change in the political
sphere turned out after all to be only one of degree.

The position Professor Kuhn adopted in his book has always appeared
to me to demand similar qualifications. According to that argument, the
differences between the kinds of change taking place during ‘normal’ and
‘revolutionary’ phases of scientific development are, at the intellectual
level, absolute. As a result, the account he gave went too far by implying
the existence of discontinuities in scientific theory far more profound and
far less explicable than any which ever in fact occur. In his new paper, he
appears to be withdrawing somewhat from that original, exposed position,
to a less extreme one; yet the effect of doing so (I shall argue) is to de-
molish entirely his original distinction between ‘normal’ and ‘revolutionary’
phases. That is evidently not his intention, but the consequence is (in my
view) inescapable.

Let me explain why I say this with the help of an analogy, taken from
the history of palaeontology during the years between 1825 and 1860.

42 STEPHEN TOULMIN

During those years, one of the two most influential palaeontological
systems was built around the theory of ‘castastrophes’, put forward first
by George Cuvier in France, and extensively developed by Louis Agassiz
at Harvard. This theory emphasized the sheer discontinuities to be found
in the geological and palaeontological record. It had the considerable
merit of challenging the bland assumption (which formed a basic methodo-
logical axiom for the followers of James Hutton, including Charles Lyell
in his early years) that all the agencies involved in geological and palaeonto-
logical change—both inorganic and organic—had been of exactly the same
kinds, and had acted in exactly the same ways, at every phase in the earth’s
history. However, Cuvier went on from his original, quite authentic
observation of geological and palaeontological discontinuities to insist
that these discontinuities were evidence of ‘super-natural’ events—that is
changes too sudden and violent to be explained in terms of natural physical
and chemical processes. The discontinuities were, as he put it, evidence
of ‘catastrophes’, and these (like the political historians’ original ‘revolu-
tions’) were something intellectually unbridgeable. When a geologist
said, ‘,.. and then there was a catastrophe’, this implied that for the change
in question no rational explanation was possible, in terms of natural
geological mechanisms such as accounted for the deposition of normal
sedimentary stratas, for example. This theoretical interpretation of the
geological and palaeontological discontinuities went too far. In some
respects, it was true, the discontinuities evidenced in the earth’s crust were
quite as sharp as Cuvier said; but as investigation proceeded it turned out
that they were neither universal in their extent nor beyond all hope of
reasonable explanation.

How was this opposition between the uniformitarian theory and the
theory of catastrophes resolved? That is the significant point for our pur-
pose here. In due course, two kinds of things happened. On the one hand,
uniformitarian geologists and palaeontologists of Lyell’s generation were
compelled, bit by bit, to acknowledge that some of the changes which
formed the subject-matter of their inquiries had in fact taken place more
drastically than they had hitherto supposed. Charles Darwin, for instance,
observed on the coast of Chile the effects of recent earthquakes which had
altered the relative location of different geological strata by as much as
20 feet in a single tremor, and this discovery convinced Lyell that past
earthquakes might, after all, have been more severe than he had previously
supposed. On the uniformitarian side, accordingly, ideas became pro-
gressively more ‘catastrophic’. Meanwhile in the catastrophist camp ideas
developed in the opposite direction. Louis Agassiz, in particular, found
his studies compelling him to multiply the number of catastrophes

DISTINCTION BETWEEN NORMALAND REVOLUTIONARY SCIENCE 43

invoked to explain the actual geological evidence, and to diminish their
size, As a result, the original ‘drastic and inexplicable’ catastrophes,
eventually became so many, and so minor, that they began to evince
uniformities, so turning into geological and palaeontological phenomena
in their own right. As such, the claim that they were not open to mech-
anistic or naturalistic explanation ceased any longer to be plausible, and
the need—even in their case—to give some kind of an account of the
mechanisms involved became unanswerable. In a word, the original
‘catastrophes’ became uniform and law-governed just like any other
geological and palaeontological phenomena. What the catastrophist palaeon-
tologists did not immediately appreciate was that this apparently innocent
change within the structure of their theory destroyed their original cri-
terion for distinguishing between ‘normal’ (or natural) and ‘catastrophic’
(or supernatural) changes in the earth’s crust, and that the very distinction
between the ‘normal and the ‘catastrophic’ had thereby collapsed.

Let me now apply this analogy. As I read Professor Kuhn’s present
account of his position, he has moved away from the original ‘normal’/
‘revolutionary’ dichotomy, in the same direction that Agassiz moved away
from Cuvier’s original theory. Once again it was both worthwhile and
important, at the outset, to insist that the development of scientific ideas
involves, at times, changes so drastic that they introduce profound con-
ceptual incongruities between the ideas accepted by successive generations
of scientists. No theory of scientific growth and development would be
adequate which did not recognize, and do justice to these intellectual
discontinuities. In Kuhn’s earlier accounts—in the 1962 book as much as
in the 1961 paper—he depicted these ‘revolutionary’ discontinuities as
being absolute. They created a situation in which there was, inevitably,
complete incomprehension at the theoretical level between supporters of
the older and newer systems of scientific thought; for example, between a
supporter of the older, Newtonian dynamics and a supporter of the new
Einsteinian dynamics. This incomprehension was inescapable because, when
it came to organizing their experience, the two men shared no common
language, no common viewpoint, nor even a common gestalt. In conse-
quence, neither the Newtonian language nor the Einsteinian language would
suffice to explain either point of view to supporters of the other. The occur-
rence of a ‘scientific revolution’ (it appeared) threw attempts at communi-
cation so completely out of joint that incomprehension was guaranteed.

Yet there was always an element of rhetorical exaggeration in this state-
ment of the matter, just as much as in Kuhn’s earlier use of the work
‘dogma’. After all, the professional careers of numerous physicists spanned
the years from 18g0 to 1930, and these men lived through the change from

44 STEPHEN TOULMIN

the Newtonian to the Einsteinian system of thought. If the complete
breakdown in scientific communication which Kuhn treats as the essential
characteristic of a scientific revolution had in fact been manifested during
this period, one should be able to document it from the experience of the
men in question, What do we find? If the conceptual change involved in
the transition was as deep as Kuhn claims, these physicists at any rate
appeared curiously unaware of the fact. On the contrary, many of them
were able to say, after the event, why they had changed their own personal
position from a classical to a relativistic one—and when I say ‘why’ I mean
‘for what reasons .. .’. Taking Kuhn at his word, however, such a change
of position could have come about only as a result of a ‘conversion’—the
sort of mind-change which a man would have to describe by saying, ‘I can
no longer see Nature as I did before . . ..—or alternatively as the outcome
of ‘causes’ rather than ‘reasons’—‘Einstein was so very persuasive ...’, or
‘I found myself changing without knowing why . ..’, or ‘It was as much as
my job was worth...’.

Accordingly, one may concede that the development of scientific thought
does involve important conceptual discontinuities, and that the conceptual
systems which displace one another within a scientific tradition may often
be based on quite different, and even incongruous principles and axioms;
but we must beware of going all the way with Kuhn’s original ‘revolu-
tionary’ hypothesis. For the displacement of one system of concepts by
another is itself something that happens for perfectly good reasons, even
though these particular ‘reasons’ cannot themselves be formalized into
still broader concepts, or still more general axioms. For what is presupposed
by both parties in such a debate—both those who cling on to the older
view, and those who put forward a new one—is not a common body of
principles and axioms: rather it is a common set of ‘selection procedures’
and ‘selection rules’, and these are not so much ‘scientific principles’ as
‘principles constitutive of science’. (They, too, may change in the course
of history, as Imre Lakatos has demonstrated in the case of the criteria of
mathematical proof, but they do so more slowly than the theories which
they are used to judge.)

Suppose, then, one concedes to Kuhn that ‘conceptual incongruities’
between the ideas of successive generations of scientists do introduce real
discontinuities into the development of scientific thought. If this is the
essence of his insight, then we shall have to go along with him down the
next leg of his argument, corresponding to the ‘modified catastrophism’ of
Agassiz. For whereas on Kuhn’s original account, scientific revolutions
were something that tended to happen in a given branch of science only
once every two hundred years or so, the ‘conceptual incongruities’ with

DISTINCTION BETWEEN NORMALAND REVOLUTIONARY SCIENCE 45

which he is now preoccupied are liable to turn up very much more fre-
quently. On a small enough scale, indeed, they are very frequent indeed;
and perhaps every new generation of scientists having any original ideas
or ‘slant’ of its own finds itself, at certain points and in certain respects, at
cross-purposes with the immediately previous generation. One may ques-
tion, indeed, whether any natural science having a serious theoretical
component ever develops by a process of ‘accretion’ alone.

In that case, however, the occurrence of a ‘scientific revolution’ no
longer amounts to a dramatic interruption in the ‘normal’ continuous
consolidation of science: instead, it becomes a mere ‘unit of variation’
within that very process of scientific change. As in palaeontology, the
hyper-rational aspect of the discontinuities vanishes, and—in the process—
the very basis for distinguishing between ‘normal’ and ‘revolutionary’
change in science which was the very heart and core of Kuhn’s theory,
collapses. For the ‘absoluteness’ of the transition involved in a scientific
revolution provided the original criterion for recognizing that one had
occurred at all. And, once we acknowledge that ne conceptual change in
science is ever absolute, we are left only with a sequence of greater and
lesser conceptual modifications differing from one another in degree. The
distinctive element in Kuhn’s theory is thus destroyed, and we are left
looking beyond it for a new sort of theory of scientific change. This theory
will have to go beyond both Kuhn’s concept of ‘revolutions’ and the naive
uniformitarian views which he renounced, just as Darwin’s evolutionary
reinterpretation of palaeontology went beyond both the catastrophism of
Cuvier and the uniformitarianism of Lyell.

Like Professor Kuhn, I believe that this new theory—when we have it—
will have to be based in part on the results of new empirical studies of the
actual development and growth of science; and that, as a result, it will
tend to bring the logic of science closer together with its sociology and
psychology. Yet it will remain as important as ever (as Sir Karl Popper
emphasizes) to avoid zdentifying the logical criteria for appraising new
scientific hypotheses with generalizations about the actual practice of
scientists, taken either individually or collectively as professional
groups.

What form should such a theory take? Once more, the experience of
other historical disciplines may give us a hint. For again and again the
fruitful direction for escaping the deadlock between revolutionary and
uniformitarian views of historical change has been the same: by way of
scrutinizing more closely the mechanisms involved, in particular, the
mechanisms of variation and perpetuation. (Compare, for instance, Charles
Darwin’s Origin of Species with Crane Brinton’s Anatomy of Revolution.)

46 STEPHEN TOULMIN

Let me pursue this hint a little way, at the price of anticipating an argu-
ment to be set out at length elsewhere.!

Suppose we stop thinking of Kuhn’s small-scale ‘micro-revolutions’ as
units of effective change in scientific theory, and treat them instead as units
of variation. We will then be faced with a picture of science in which the
theories currently accepted at each stage serve as starting-points for a
large number of suggested variants; but in which only a small fraction of
these variants in fact survive and become established within the body of
ideas passed on to the next generation. The single question, ‘How do
revolutions occur in science?’ thus has to be reformulated, and gives rise
to two distinct groups of questions. On the one hand we must ask, “What
factors determine the number and nature of theoretical variants proposed
for consideration in a particular science during a given period?’ the counter-
part, in biological evolution, to the genetical question about the origin of
mutant forms. On the other hand we must ask, ‘What factors and considera-
tions determine which intellectual variants win acceptance, to become
established in the body of ideas which serves as the starting-point for the next
round of variations?’ the counterpart to biological questions aboutselection.

As in other historical disciplines, accordingly, the problem of historical
change can usefully be restated as a problem of variation-and-selective-
perpetuation. The advantages of such a restatement cannot be fully
expounded here, but one thing at any rate is worth indicating. It not only
helps us to locate the ambiguity which drives the debate between Kuhn
and Popper into cross-purposes—the ambiguity between the philosophy
of science, which is concerned with the question what consideration
should properly determine the selection between new variants, and the
psychology or sociology of science, which is concerned with the considera-
tions that in fact settle the matter. It can also, I believe, help us to resolve
some of the old perplexities about the relationship between external and
internal factors in the development of an intellectual tradition. If scientific
change is treated as a special case of a more general phenomenon of
‘conceptual evolution’, we can distinguish at least three different aspects
of this evolution. The actual bulk, or quantity, of innovation going on in a
given field at any time can be distinguished from the direction in which this
innovation is predominantly tending; and both of these can be distin-
guished, in turn, from the selection criteria determining which variants are
perpetuated within the tradition.

Once these distinctions are clearly made, it will be desirable to consider
separately how far each aspect of scientific change is responsive either to

1 See my [1966] for a brief analysis. The full exposition will be given in a forthcoming
book on conceptual evolution and the problem of ‘human understanding’.

DISTINCTION BETWEEN NORMAL AND REVOLUTIONARY SCIENCE 47

internal or to external factors, and it will become naive to suppose that
there need be any conflict between the two kinds of account. As a hint: the
volume of innovation going on in any science presumably depends to a
great extent on the opportunities provided in that social context for doing
original work on the science in question—hence, the rate of innovation will
be substantially responsive to factors external to science. On the other hand,
the selection-criteria for appraising conceptual innovations in science will
be very largely a professional and so an internal matter: many scientists,
indeed, would expect them to be entirely an internal, professional matter—
though this may, in practice, be no more than an unrealizable ideal.
Finally, the direction of innovation in a particular science depends on a
complex mixture of factors, internal and external: the sources of novel
hypotheses are highly varied, and subject to influences and analogies
remote from the detailed problems in hand.

The fuller ramifications of an ‘evolutionary’ theory of scientific change
(as contrasted with Kuhn’s ‘catastrophism’) must be held over for another
occasion. For the moment, let me end with two questions, which will help
to pin-point the transitional character of Kuhn’s present position. (1) How
extensive do the conceptual incongruities between the ideas of one scien-
tific generation and those of the next have to be, if the transition between
them is to constitute a ‘scientific revolution’ on Kuhn’s present account?
(I assume that none was ever, in fact, extensive enough to satisfy his
original criterion; so we now need a new criterion to replace it.) (2) If any
conceptual shift between the theories of successive generations capable of
provoking incomprehension between them is to be accepted as a ‘revolu-
tion’, then can we not demand a general account of the role of all such
conceptual shifts within the development of scientific thought? Are we not
entitled, in a phrase, to treat these ‘micro-revolutions’ as the counterparts
of the ‘micro-catastrophes’ of Agassiz and the later catastrophist geolo-
gists? And, if that is the case, are we not in fact entirely outgrowing the
original implications of the term ‘revolution’? Students of political history
have by now outgrown any naive reliance on the idea of ‘revolutions’. If I
am right, and the ‘micro-revolutions’ of Kuhn’s present position are the
units of all scientific innovation, then the idea of ‘scientific revolution’ will
have to follow that of ‘political revolutions’ out of the category of explan-
atory concepts and into that of mere descriptive labels.

REFERENCES

Collingwood [1940] An Essay on Metaphysics, 1940.

Crombie (ed.) [1963]: Scientific Change, 1963.

Toulmin [1966]: ‘Conceptual Revolutions in Science’, in Cohen-Wartofsky (eds.): Boston
Studies in the Philosophy of Science, 3, 1967, pp. 331-47.

Normal Science, Scientific Revolutions
and the History of Science

L. PEARCE WILLIAMS
Cornell University

I should like to comment very briefly on the Kuhn-Popper disagreement
over the essential nature of science and the genesis of scientific revolutions.
If I understand Sir Karl Popper correctly, science is basically and con-
stantly potentially on the verge of revolution. A refutation, at least if it is
big enough, constitutes such a revolution. Professor Kuhn argues, on the
other hand, that most of the time devoted to the pursuit of science is what
he calls ‘normal’ science—that is, problem solving, or working out chains
of argument implicit in previous work. Thus, for Kuhn, a scientific
revolution is a long time a-building and occurs only rarely because most
people are not trying to refute current theories. Both sides have presented
their positions in considerable detail but there seems to me to be a very
important gap in both theories. It is, simply, how do we know what
science is all about? The question may sound startlingly naive, but I shall
now attempt to justify it.

There are, essentially, two respectable scholarly ways to go about
answering the question. One is sociological; the scientific community may
be treated like any other community and subjected to sociological analysis.
Note that this ‘may’ be done, but that it has not yet been done. To put it
another way, most scientific activity may be directed toward refutation or
toward ‘problem solving’, but we don’t know whether it is or not. I may
just interject here that I am not impressed with Miss Masterman’s observa-
tion that the paradigm is eagerly grasped by researchers in such fieids as
computer science and the social sciences. After all, the figure of the drown-
ing man and the straw is a familiar one. I do not believe that Dr Kuhn
intended to restrict his analysis to embryo sciences and I am interested in
what practitioners of mature sciences think they are doing. To repeat, we
simply do not have this information. The difficulties in the way of com-
piling it are enormous. Do we want simply a quantitative sample? Is what
most scientists do really relevant to what science, in the long run, is? Do
we weight the opinion of, say, Peter Debye equally with that of a man who
accurately measures nuclear cross-sections? I am no sociologist, but I
should think that approaching the problem through sociology would be to
tun a course filled with thorns.

50 L. PEARCE WILLIAMS

Yet it should be noted that both Kuhn and Popper base their systems on
(in Kuhn’s case) what scientists do (with no hard evidence that they do do
science this way) or (in Popper’s case) on what they ought to do (with very
few examples to persuade us that this is right). Both Kuhn and Popper
really base their views of the structure of science on the history of science
and the main point of my remarks here is that the history of science cannot
bear such a load at this time. We simply do not know enough to permit a
philosophical structure to be erected on a historical foundation. For ex-
ample, there could be no better illustration of ‘normal’ science than the
experimental researches in electricity of Michael Faraday in the 1830s.
Beginning with the ‘accidental’ discovery of electromagnetic induction in
1831, each new step seemed to follow clearly from the previous one. Here
was puzzle-solving with a vengeance. This is the traditional view of Faraday,
master experimentalist who, if one reads Tyndall or even Thompson, never
had a theoretical idea in his life. Yet, the minute one moves behind the
published papers to the Diary and the manuscript notes and letters, a
strange Faraday emerges. From 1821 on he was testing fundamental
hypotheses on the nature of matter and force. How many ‘normal’ scientists
(as defined by their published papers) are really revolutionaries at heart?
Hopefully, some day the history of science will be able to answer this,
but as of now, no one can say.

Before I give too much comfort to the followers of Popper, I should like
to raise before them the spectre of the history of spectroscopy between
1870 and 1900. I think it fair to describe this period as one of mapping, in
which the spectra of the elements were described with every increasing
precision. There is precious little ‘refutation’ going on here, yet it would be
hard to deny Angstrom the title of scientist. Nor should it be forgotten
that one of the most successful ‘problem solvers’ in the history of science
was Max Planck who was also the most reluctant revolutionary of all time.

As a historian, then, I must view both Popper and Kuhn with a some-
what jaundiced eye. Both have raised issues of fundamental importance;
both have provided deep insights into the nature of science; but neither
has amassed sufficient hard evidence to lead me to believe that the essence
of the scientific quest has been captured. I shall continue to use both as
guides to my researches, always keeping in mind Lord Bolingbroke’s re-
mark that ‘history is philosophy teaching by example.’ We need a lot more
examples.

Normal Science and its Dangers

KARL POPPER
London School of Economics

Professor Kuhn’s criticism of my views about science is the most in-
teresting one I have so far come across. There are, admittedly, some points,
more or less important, where he misunderstands me or misinterprets
me. For example, Kuhn quotes with disapproval a passage from the
beginning of the first chapter of my book, The Logic of Scientific Discovery.
Now I should like to quote a passage overlooked by Kuhn, from the
Preface to the First Edition. (In the first edition the passage stood immed-
iately before the passage quoted by Kuhn; later I inserted the Preface to
the English Edition between these two passages.) While the brief passage
quoted by Kuhn may, out of context, sound as if I had been quite unaware
of the fact, stressed by Kuhn, that scientists necessarily develop their
ideas within a definite theoretical framework, its immediate predecessor
of 1934 almost sounds like an anticipation of this central point of Kuhn’s.
After two mottos taken from Schlick and from Kant, my book begins
with the following words: ‘A scientist engaged in a piece of research,
say in physics, can attack his problem straight away. He can go at once
to the heart of the matter: that is, to the heart of an organized structure.
For a structure of scientific doctrines is already in existence; and with it,
a generally accepted problem-situation. This is why he may leave it to
others to fit his contribution into the framework of scientific knowledge.’
I then go on to say that the philosopher finds himself in a different position.
Now it seems pretty clear that the passage quoted describes the ‘normal’
situation of a scientist in a way very similar to Kuhn: there is an edifice, an
organized structure of science which provides the scientist with a generally
accepted problem-situation into which his own work can be fitted. This
seems very similar to one of Kuhn’s main points: that ‘normal’ science,
as he calls it, or the ‘normal’ work of a scientist, presupposes an organized
structure of assumptions, or a theory, or a research programme, needed
by the community of scientists in order to discuss their work rationally.
The fact that Kuhn overlooked this point of agreement and that he
fastened on what came immediately after, and what he thought was a point
of disagreement, seems to me significant. It shows that one never reads
or understands a book except with definite expectations in one’s mind.
This indeed may be regarded as one of the consequences of my thesis

52 KARL POPPER

that we approach everything in the light of a preconceived theory. So also a
book. As a consequence one is liable to pick out these things which one
either likes or dislikes or which one wants for other reasons to find in the
book; and so did Kuhn when reading my book.

Yet in spite of such minor points, Kuhn understands me very well—
better, I think, than most critics of mine I know of; and his two main
criticisms are very important.

The first of these criticisms is, briefly, that I have completely overlooked
what Kuhn calls ‘normal’ science, and that I have been exclusively
engaged in describing what Kuhn calls ‘extraordinary research’, or
‘extraordinary science’.

I think that the distinction between these two kinds of enterprise
is perhaps not quite as sharp as Kuhn makes it; yet I am very ready to
admit that I have at best been only dimly aware of this distinction; and
further, that the distinction points out something that is of great im-
portance.

This being so it is a minor matter, comparatively, whether or not
Kuhn’s terms ‘normal’ science and ‘extraordinary science’ are somewhat
question begging, and (in Kuhn’s sense) ‘ideological’. I think that they
are all this; but this does not diminish my feelings of indebtedness to
Kuhn for pointing out the distinction, and for thus opening my eyes
to a host of problems which previously I had not seen quite clearly.

‘Normal’ science, in Kuhn’s sense, exists. It is the activity of the non-
revolutionary, or more precisely, the not-too-critical professional: of the
science student who accepts the ruling dogma of the day; who does
not wish to challenge it; and who accepts a new revolutionary theory only
if almost everybody else is ready to accept it—if it becomes fashionable
by a kind of bandwagon effect. 'To resist a new fashion needs perhaps as
much courage as was needed to bring it about.

You may say, perhaps, that in so describing Kuhn’s ‘normal’ science,
I am implicitly and surreptitiously criticizing him. I shall therefore
state again that what Kuhn has described does exist, and that it must be
taken into account by historians of science. That it is a phenomenon which
I dislike (because I regard it as a danger to science) while he apparently
does not dislike it (because he regards it as ‘normal’) is another question;
admittedly, a very important one.

f'In my view the ‘normal’ scientist, as Kuhn describes him, is a person
one ought to be sorry for. (Aceording to Kuhn’s views about the history of
science, many great scientists must have been ‘normal’; yet since I do

not feel sorry for them, I do not think that Kuhn’s views can be quite

right.) The ‘normal’ scientist, in my view, has been taught badly. I

NORMAL SCIENCE AND ITS DANGERS 53

believe, and so do many others, that all teaching on the University level
(and if possible below) should be training and encouragement in critical
thinking. The ‘normal’ scientist, as described by Kuhn, has been badly
taught. He has been taught in a dogmatic spirit: he is a victim of in-
doctrination. He has learned a technique which can be applied without
asking for the reason why (especially in quantum mechanics). As a
consequence, he has become what may be called an applied scientist, in
contradistinction to what I should call a pure scientist. He is, as Kuhn
puts it, content to solve ‘puzzles’.1 The choice of this term seems to
indicate that Kuhn wishes to stress that it is not a really fundamental
problem which the ‘normal’ scientist is prepared to tackle: it is, rather,
a routine problem, a problem of applying what one has learned: Kuhn
describes it as a problem in which a dominant theory (which he calls a
‘paradigm’) is applied. The success of the ‘normal’ scientist consists,
entirely, in showing that the ruling theory can be properly and satis-
factorily applied in order to reach a solution of the puzzle in question.

Kuhn’s description of the ‘normal’ scientist vividly reminds me of a
conversation I had with my late friend, Philip Frank, in 1933 or there-
abouts. Frank at that time bitterly complained about the uncritical
approach to science of the majority of his Engineering students. They
merely wanted to ‘know the facts’. Theories or hypotheses which were not
‘generally accepted’ but problematic, were unwanted: they made the
students uneasy. These students wanted to know only those things, those
facts, which they might apply with a good conscience, and without heart-
searching.

I admit that this kind of attitude exists; and it exists not only among
engineers, but among people trained as scientists. I can only say that I
see a very great danger in it and in the possibility of its becoming normal
(just as I see a great danger in the increase of specialization, which also
is an undeniable historical fact): a danger to science and, indeed, to
our civilization. And this shows why I regard Kuhn’s emphasis on the
existence of this kind of science as so important.

I believe, however, that Kuhn is mistaken when he suggests that what
he calls ‘normal’ science is normal.

Of course, I should not dream of quarrelling about a term. But I
wish to suggest that few, if any, scientists who are recorded by the history

1 [ do not know whether Kuhn’s use of the term ‘puzzle’ has anything to do with Wittgen-
stein’s use, Wittgenstein, of course, used it in connection with his thesis that there are no
genuine problems in philosophy—only puzzles, that is to say, pseudo-problems connected
with the improper use of language. However this may be, the use of the term ‘puzzle’

instead of ‘problem’ is certainly indicative of a wish to show that the problems so described
are not very serious or very deep.

54 KARL POPPER

of science were ‘normal’ scientists in Kuhn’s sense. In other words, I
disagree with Kuhn both about some historical facts, and about what is
characteristic for science.

Take as an example Charles Darwin before the publication of The
Origin of Species. Even after this publication he was what might be des-
cribed as a ‘reluctant revolutionary’, to use Professor Pearce Williams’s
beautiful description of Max Planck; before it he was hardly a revolution-
ary at all. There is nothing like a conscious revolutionary attitude in
his description of The Voyage of the Beagle. But it is brim full of problems;
of genuine, new and fundamental problems, and of ingenious conjectures—
conjectures which often compete with each other—about possible solutions.

There can be hardly a less revolutionary science than descriptive
botany. Yet the descriptive botanist is constantly faced with genuine
and interesting problems: problems of distribution, problems of character-
istic locations, problems of species or sub-species differentiation, problems
like those of symbiosis, characteristic enemies, characteristic diseases,
resistant strains, more or less fertile strains, and so on. Many of these
descriptive problems force upon the botanist an experimental approach;
and this leads on to plant physiology and thus to a theoretical and ex-
perimental (rather than purely ‘descriptive’) science. The various stages of
these transitions merge almost imperceptibly, and genuine problems
rather than ‘puzzles’ arise at every stage.

But perhaps Kuhn calls a ‘puzzle’ what I should call a ‘problem’;
and surely, we do not want to quarrel about words. So let me say some-
thing more general about Kuhn’s typology of scientists.

Between Kuhn’s ‘normal scientist’ and his ‘extraordinary scientist’
there are, I assert, many gradations; and there must be. Take Boltzmann:
there are few greater scientists. But his greatness can hardly be said
to consist in his having staged a major revolution for he was, to a con-
siderable extent, a follower of Maxwell. But he was as far from a ‘normal
scientist’ as anybody could be: he was a valiant fighter who resisted the
ruling fashion of his day—a fashion which, incidentally, ruled only on
the continent and had few adherents, at that time, in England.

I believe that Kuhn’s idea of a typology of scientists and of scientific
periods is important, but that it needs qualification. His schema of ‘normal’
periods, dominated by one ruling theory (a ‘paradigm’ in Kuhn’s termin-
ology) and followed by exceptional revolutions, seems to fit astronomy
fairly well. But it does not fit, for example, the evolution of the theory of
matter; or of the biological sciences since, say, Darwin and Pasteur. In
connection with the problem of matter, more especially, we have had at
least three dominant theories competing since antiquity: the continuity

NORMAL SCIENCE AND ITS DANGERS 55

theories, the atomic theories, and those theories which tried to combine
the two. In addition, we had for a time Mach’s version of Berkeley—the
theory that ‘matter’ was a metaphysical rather than a scientific concept:
that there was no such thing as a physical theory of the structure of matter;
and that the phenomenological theory of heat should become the one
paradigm of all physical theories. (I am using here the word ‘paradigm’
in a sense slightly different from Kuhn’s usage: to indicate not a dominant
theory, but rather a research programme—a mode of explanation which is
considered so satisfactory by some scientists that they demand its general
acceptance.)

Although I find Kuhn’s discovery of what he calls ‘normal’ science
most important, I do not agree that the history of science supports his
doctrine (essential for his theory of rational communication) that ‘normally’
we have one dominant theory—a ‘paradigm’—in each scientific domain,
and that the history of a science consists in a sequence of dominant
theories, with intervening revolutionary periods of ‘extraordinary’ science;
periods which he describes as if communication between scientists had
broken down, owing to the absence of a dominant theory.

This picture of the history of science clashes with the facts as I see them.
For there was, ever since antiquity, constant and fruitful discussion be-
tween the competing dominant theories of matter.

Now in his present paper, Kuhn seems to propose the thesis that the
logic of science has little interest and no explanatory power for the historian
of science.

It seems to me that coming from Kuhn this thesis is almost as para-
doxical as the thesis ‘I do not use hypotheses’ was when it was pronounced
in Newton’s Optics. For as Newton used hypotheses, so Kuhn uses
logic—not merely in order to argue, but precisely in the same sense in
which I speak of the Logic of Discovery. He uses, however, a logic of
discovery which in some points differs radically from mine: Kuhn’s
logic is the logic of historical relativism.

Let me first mention some points of agreement. I believe that science
is essentially critical; that it consists of bold conjectures, controlled by
criticism, and that it may, therefore, be described as revolutionary. But
I have always stressed the need for some dogmatism: the dogmatic
scientist has an important role to play. If we give in to criticism too easily,
we shall never find out where the real power of our theories lies.

But this kind of dogmatism is not what Kuhn wants. He believes in
the domination of a ruling dogma over considerable periods; and he does
not believe that the method of science is, normally, that of bold conjectures
and criticism.

56 KARL POPPER

What are his main arguments? They are not psychological or historical—
they are logical: Kuhn suggests that the rationality of science presupposes
the acceptance of a common framework. He suggests that rationality
depends upon something like a common language and a common set of
assumptions. He suggests that rational discussion, and rational criticism,
is only possible if we have agreed on fundamentals.

This is a widely accepted and indeed a fashionable thesis: the thesis
of relativism. And it is a logical thesis.

I regard the thesis as mistaken. I admit, of course, that it is much
easier to discuss puzzles within an accepted common framework, and to
be swept along by the tide of a new ruling fashion into a new framework,
than to discuss fundamentals—that is, the very framework of our assump-
tions. But the relativistic thesis that the framework cannot be critically
discussed is a thesis which can be critically discussed and which does not
stand up to criticism.

I have dubbed this thesis The Myth of the Framework, and I have
discussed it on various occasions. I regard it as a logical and philosophical
mistake. (I remember that Kuhn does not like my usage of the word
‘mistake’; but this dislike is merely part of his relativism.)

I should like just to indicate briefly why I am not a relativist:1 I do
believe in ‘absolute’ or ‘objective’ truth, in Tarski’s sense (although
I am, of course, not an ‘absolutist’ in the sense of thinking that I, or
anybody else, has the truth in his pocket). I do not doubt that this is
one of the points on which we are most deeply divided; and it is a logical
point.

[ I do admit that at any moment we are prisoners caught in the framework
of our theories; our expectations; our past experiences; our language.
But we are prisoners in a Pickwickian sense: if we try, we can break out
of our framework at any time. Admittedly, we shall find ourselves again
in a framework, but it will be a better and roomier one; and we can at
any moment break out of it again.4

The central point is that a critical discussion and a comparison of
the various frameworks is always possible. It is just a dogma—a dangerous
dogma—that the different frameworks are like mutually untranslatable
languages. The fact is that even totally different languages (like English
and Hopi, or Chinese) are not untranslatable, and that there are many
Hopis or Chinese who have learnt to master English very well.

The Myth of the Framework is, in our time, the central bulwark of
irrationalism. My counter-thesis is that it simply exaggerates a difficulty

1 See, for example, Chapter 10 of my Conjectures and Refutations, and the first Addendum
to the 4th (1962) and later editions of volume ii of my Open Society.

NORMAL SCIENCE AND ITS DANGERS 57

into an impossibility. The difficulty of discussion between people brought
up in different frameworks is to be admitted. But nothing is more fruitful
than such a discussion; than the culture clash which has stimulated some
of the greatest intellectual revolutions.

I admit that an intellectual revolution often looks like a religious con-
version. A new insight may strike us like a flash of lightning. But this
does not mean that we cannot evaluate, critically and rationally, our
former views, in the light of new ones.

It would thus be simply false to say that the transition from Newton’s
theory of gravity to Einstein’s is an irrational leap, and that the two are
not rationally comparable. On the contrary, there are many points of
contact (such as the role of Poisson’s equation) and points of comparison:
it follows from Einstein’s theory that Newton’s theory is an excellent
approximation (except for planets or comets moving on elliptic orbits
with considerable eccentricities).

Thus in science, as distinct from theology, a critical comparison of the
competing theories, of the competing frameworks, is always possible.
And the denial of this possibility is a mistake. In science (and only in
science) can we say that we have made genuine progress: that we know
more than we did before.

Thus the difference between Kuhn and myself goes back, fundamentally,
to logic. And so does Kuhn’s whole theory. To his proposal: ‘Psychology
rather than Logic of Discovery’ we can answer: all your own arguments
go back to the thesis that the scientist is logically forced to accept a frame-
work, since no rational discussion is possible between frameworks. This
is a logical thesis—even though it is mistaken.

Indeed, as I have explained elsewhere, ‘scientific knowledge’ may be
regarded as subjectless.1 It may be regarded as a system of theories on
which we work as do masons on a cathedral. The aim is to find theories
which, in the light of critical discussion, get nearer to the truth. Thus
the aim is the increase of the truth-content of our theories (which, as I
have shown,? can be achieved only by increasing their content).

I cannot conclude without pointing out that to me the idea of turning
for enlightenment concerning the aims of science, and its possible progress,
to sociology or to psychology (or, as Pearce Williams recommends, to the
history of science) is surprising and disappointing.

In fact, compared with physics, sociology and psychology are riddled

1 See now my lecture ‘Epistemology Without a Knowing Subject’ in Proceedings of the
Third International Congress for Logic, Methodology and Philosophy of Science, Amsterdam
1967.

® See my paper ‘A Theorem on Truth-Content’ in the Feigl Festschrift Mind, Matter,
and Method, edited by P. K. Feyerabend and Grover Maxwell, 1966.

58 KARL POPPER

with fashions, and with uncontrolled dogmas. The suggestion that we can
find anything here like ‘objective, pure description’ is clearly mistaken.
Besides, how can the regress to these often spurious sciences help us in
this particular difficulty? Is it not sociological (or psychological, or histor-
ical) science to which you want to appeal in order to decide what amounts
to the question ‘What is science?’ or ‘What is, in fact, normal in science?”
For clearly you do not want to appeal to the sociological (or psychological
or historical) lunatic fringe? And whom do you want to consult: the
‘normal’ sociologist (or psychologist, or historian) or the ‘extraordinary’
one?

This is why I regard the idea of turning to sociology or psychology as
surprising. I regard it as disappointing because it shows that all I have
said before against sociologistic and psychologistic tendencies and ways,
especially in history, was in vain.

No, this is not the way, as mere logic can show; and thus the answer
to Kuhn’s question ‘Logic of Discovery or Psychology of Research?” is
that while the Logic of Discovery has little to learn from the Psychology
of Research, the latter has much to learn from the former.

The Nature of a Paradigm’

MARGARET MASTERMAN
Cambridge Language Research Unit

1. The initial difficulty: Kuhn’s multiple definitions of a paradigm.

2. The originality of Kuhn’s sociological notion of a paradigm: the paradigm
is something which can function when the theory is not there.

3. The philosophic consequence of Kuhn’s insistence on the centrality of
normal science: philosophically speaking, a paradigm is an artefact which
can be used as a puzzle-solving device; not a metaphysical world-view.

4. A paradigm has got to be a concrete ‘picture’ used analogically; because it
has got to be a ‘way of seeing’.

5. Conclusion: preview of the logical characteristics of a paradigm.

The purpose of this paper is to elucidate T. S. Kuhn’s conception of a
paradigm; and it is written on the assumption that 'T’. S. Kuhn is one of the
outstanding philosophers of science of our time.

It is curious that, up to now, no attempt has been made to elucidate this
notion of paradigm, which is central to Kuhn’s whole view of science as
set out in his [1962].? Perhaps this is because this book is at once scienti-
fically perspicuous and philosophically obscure. It is being widely read,
and increasingly appreciated, by actual research workers in the sciences,
so that it must be (to a certain extent) scientifically perspicuous. On the
other hand, it is being given widely diverse interpretations by philosophers,
which gives some reason to think that it is philosophically obscure. The
reason for this double reaction, in my view, derives from the fact that
Kuhn has really looked at actual science, in several fields, instead of con-
fining his field of reading to that of the history and philosophy of science,
i.e. to one field. Insofar, therefore, as his material is recognizable and
familiar to actual scientists, they find his thinking about it easy to under-
stand. In so far as this same material is strange and unfamiliar to

1 This paper is a later version of an earlier paper which I had been asked to read when
there was to have been a panel discussion of T. S. Kuhn’s work in this Colloquium; and
which I was prevented from writing by getting severe infective hepatitis. This new version
is therefore dedicated to the doctors, nurses and staff of Block 8, Norwich Hospital, who
allowed a Kuhn subject-index to be made on a hospital bed.

It has been tailored in shape to conform, as closely as possible, to the convalescent
contribution which I actually made from the floor at the Symposium.

2 The view presented in this paper is based on Kuhn’s [1962], not on the rest of his
published work. All page-numbers given in the text refer to Kuhn’s [1962].

60 MARGARET MASTERMAN

philosophers of science, they find any thinking that is based on it opaque.
Kuhn’s form of thinking, however, is not in fact opaque, but complex,
since, philosophically | speaking, it reflects the complexity of its material.
In an analogous way Lakatos, in Proofs and Refutations' has introduced a
new complexity and realism into our conception of mathematics, because
he has taken a close look at what mathematicians really do when they
refine and change each other’s devices and ideas. As philosophers, there-
fore, we ought to progress beyond the new ‘point of realism’ about science
these two have established, not regress from it. And as scientists, we ought
to examine closely the work of both these two detailed thinkers, since, even
if only as a general guide, it might be of use actually within science.

The present Peper is written more ges a scientific point of of view thar than a
physical, but in ‘the computer sciences, That being so, far from querying
the existence of Kuhn’s ‘normal science’, I am going to assume it. There is
no need to keep on invoking history here. That there is normal science—
and that it is exactly as Kuhn says it is—is the outstanding, the crashingly
obvious fact which confronts and hits any philosophers of science who set
out, in a practical or technological manner, to do any actual scientific re-
search. It is because Kuhn—at last—has noticed this central fact about all
real science (basic research, applied, technological, are all alike here),
namely that it is normally a habit-governed, puzzle-solving activity, not a
fundamentally upheaving or falsifying activity (not, in other words, a
philosophical activity), that actual scientists are now, increasingly reading
Kuhn instead of Popper: to such an extent, indeed, that, in new scientific
fields particularly, ‘paradigm’ and not ‘hypothesis’ is now the ‘O.K. word’.
It is thus scientifically urgent, as well as philosophically important, to try
to find out what a Kuhnian paradigm is.

Since my overall viewpoint is scientific, this paper also assumes that
science as it is actually done—i.e. science roughly as Kuhn describes it—
is also science as it ought to be done. For if there is not some self-correcting
mechanism which operates within science itself, then there is no hope that,
scientifically speaking, things ever will be set right when they go wrong.
For the one thing working scientists are not going to do is to change their
ways of thinking, in doing science, ex more philosophico, because they have
Popper and Feyerabend pontificating at them like eighteenth-century
divines; particularly as both Popper and Feyerabend normally pontificate
at even more than eighteenth-century length.”

1 Lakatos [1963-4].

2 Feyerabend [1962], p. 60. (This more-than-prophetic outburst includes within itself a
meta-outburst against contemporary linguistic Oxford philosophy.) See also, more briefly,
Watkins in the present symposium.

THE NATURE OF A PARADIGM 61

This preface is, I fear, a shade aggressive; compression of material and
indignation with what I shall call in the paper ‘philosophy-of-science-
aetherialism’ have caused this. In any case, in view especially of some of the
more extreme phrases used by Watkins,! a little pro-Kuhn aggressiveness
injected into this symposium will not do any harm.

I. THE INITIAL DIFFICULTY: KUHN’S MULTIPLE DEFINITIONS OF A
PARADIGM

Two vital difficulties arise for those who take Kuhn’s ‘new image of
science”? seriously. On the first, which is his conception of verification in
experience (or the absence of it), I do not agree with him and on this it
seems to me that the philosophical empiricist world has indeed a case
against him. But on the second, which is his conception of a paradigm, he
has a case against them. For not only is Kuhn’s paradigm, in my view, a

fundamental idea and.a new one in the philosophy of science, and therefore
one which deserves 3 examination, but also, although Kuhn’s whole general
view of the nature of scientific revolutions depends on it, those who attack
him have never taken the trouble to find out what itis. Instead, they assume
without question either her that a paradigm is a ‘basic theory’ or that it is a
‘general metaphysical viewpoint’; whereas I think it is in fact quite easy to

_show that, in its primary sense, it cannot be either of these.

Kuhn, of course, with that quasi-poetic style of his, makes paradigm-
elucidation genuinely difficult for the superficial reader. On my counting,
he uses ‘paradigm’ in not less than ‘twenty-one different senses in his
[1962], possibly more, not less. Thus he describes a paradigm:

(1) as a universally recognized scientific achievement (p. x): ‘[Paradigms] I take
to be universally recognized scientific achievements that for a time provide model
problems and solutions to a community of practitioners’.

(z) As a myth (p. 2): ‘Historians confront growing difficulties in distinguishing
the ‘scientific’ component of past observation and belief from what their predecessors
had readily labelled ‘error’ and ‘superstition’. The more carefully they study, say,
Aristotelian dynamics, phlogistic chemistry, or caloric thermodynamics, the more

1 For example, in the comparison between Kuhn’s view of ‘the scientific community as
an essentially closed society, intermittently shaken by collective nervous breakdowns
followed by restored mental unison’, and Popper’s (noble) view of it as an open society;
see Watkins, this volume, p. 26, footnote 2 and pp. 29-30. The latter contains a really very
gross distortion of Kuhn’s real view—a distortion repeated on pp. 31-32, and in the whole
tone of the passage, accusing Kuhn of ‘seeing science as the scientist’s religion’; and in
that of his discussion of what he calls ‘The Instant-Paradigm Thesis’. It is only fair to say
that Watkins also apologizes twice for the unnecessary violence of his style; once when he
correctly accuses himself of ‘a certain conscious unfairness’; and once when he confesses
to speaking ‘a trifle maliciously’. But that a serious philosopher of his calibre should con-
sider himself justified in being concurrently thus superficial and inaccurate in criticism, and
thus violent in style—this is not only matter for comment, but also for surprise.

? Kuhn [1962], pp. 1 and 3.

62 MARGARET MASTERMAN

certain they feel that those once current views of nature were, as a whole, neither
less scientific nor more the product of human idiosyncrasy than those current
today. If these out-of-date beliefs are to be called myths, then myths can be produced
by the same sorts of methods and held for the same sorts of reasons that now lead to
scientific knowledge. If, on the other hand, they are to be called science, then science
has included bodies of belief quite incompatible with the ones we hold today.’

(3) Asa ‘philosophy’, or constellation of questions (pp. 4-5): ‘[No] scientific group
could practise its trade without some set of received beliefs. Nor does it make less
consequential the particular constellation to which the group, at a given time, is in
fact committed. Effective research scarcely begins before a scientific community
thinks it has acquired firm answers to questions like the following: What are the
fundamental entities of which the universe is composed? How do these interact with
each other and with the senses? What questions may legitimately be asked about
such entities and what techniques employed in seeking solutions?’.

(4) As a textbook, or classic work (p. 10): ‘ ‘‘Normal science” means research
firmly based upon one or more past scientific achievements, achievements that
some particular scientific community acknowledges for a time as supplying the
foundation for its further practice. Today such achievements are recounted,
though seldom in their original form, by science textbooks, elementary and advanced.
‘These textbooks expound the body of accepted theory, illustrate many or all of its
successful applications, and compare these applications with exemplary observa-
tions and experiments. Before such books became popular early in the nineteenth
century (and until even more recently in the newly matured sciences), many of the
famous classics of science fulfilled a similar function. Aristotle’s Physica, Ptolemy’s
Almagest, Newton’s Principia and Opticks, Franklin’s Electricity, Lavoisier’s
Chemistry, and Lyell’s Geology—these and many other works served for a time
implicitly to define the legitimate problems and methods of a research field for
succeeding generations of practitioners. They were able to do so because they
shared two essential characteristics. Their achievement was sufficiently unprece-
dented to attract an enduring group of adherents away from competing modes
of scientific activity. Simultaneously, it was sufficiently open-ended to leave all
sorts of problems for the redefined group of practitioners to resolve. Achievements
that share these two characteristics I shall henceforth refer to as “‘paradigms’’.’
(5) As a whole tradition, and in some sense, as a model (pp. 10-11): ‘.. . some
accepted examples of actual scientific practice—examples which include law,
theory, application, and instrumentation together—provide models from which
spring particular coherent traditions of scientific research. These are the traditions
which the historian describes under such rubrics as ‘‘Ptolemaic astronomy” (or
“Copernican”’), ‘Aristotelian dynamics” (or ““Newtonian”), “corpuscular optics”
(or “wave optics”), and so on. The study of paradigms, including many that are
far more specialised than those named illustratively above, is what mainly prepares
the student for membership in the particular scientific community with which he
will later practise.’

(6) As a scientific achievement (p. 11): ‘Because in this essay the concept of a para-
digm will often substitute for a variety of familiar notions, more will need to be said
about the reasons for its introduction. Why is the concrete scientific achievement,
as a locus of professional commitment, prior to the various concepts, laws, theories,
and points of view that may be abstracted from it? In what sense is the shared
paradigm a fundamental unit for the student of scientific development, a unit that

THE NATURE OF A PARADIGM 63

cannot be fully reduced to logically atomic components which might function in
its stead?’

(7) As an analogy (p. 14): ‘One early group of theories, following seventeenth-
century practice, regarded attraction and frictional generation as the fundamental
electrical phenomena. This group tended to treat repulsion as a secondary effect
due to some sort of mechanical rebounding and also to postpone for as long as
possible both discussion and systematic research on Gray’s newly discovered effect,
electrical conduction. Other “electricians” (the term is their own) took attraction
and repulsion to be equally elementary manifestations of electricity and modified
their theories and research accordingly. (Actually, this group is remarkably small—
even Franklin’s theory never quite accounted for the mutual repulsion of two
negatively charged bodies.) But they had as much difficulty as the first group in
accounting simultaneously for any but the simplest conduction effects. Those
effects, however, provided the starting point for still a third group, one which
tended to speak of electricity as a ‘fluid’ that could run through conductors rather
than as an “effluvium” that emanated from non-conductors.’

(8) As a successful metaphysical speculation (pp. 17-18): ‘.. . in the early stages
of the development of any science different men confronting the same range of
phenomena, but not usually all the same particular phenomena, describe and
interpret them in different ways. What is surprising, and perhaps also unique in
its degree to the fields we call science, is that such initial divergences should ever
largely disappear . . . 'To be accepted as a paradigm, a theory must seem better than
its competitors, but it need not, and in fact never does, explain all the facts with
which it can be confronted.’

(9) As an accepted device in common law (p. 23): ‘In its established usage, a para-
digm is an accepted model or pattern, and that aspect of its meaning has enabled
me, lacking a better word, to appropriate “paradigm” here. But it will shortly be
clear that the sense of “model”? and “pattern” that permits the appropriation is
not quite the one usual in defining “‘paradigm’’. In grammar, for example, ‘amo,
amas, amat’’ is a paradigm because it displays the pattern to be used in conjugating
a large number of other Latin verbs, e.g. in producing “Jaudo, laudas, laudat’’.
In this standard application, the paradigm functions by permitting the replication
of examples any one of which could in principle serve to replace it. In a science, on
the other hand, a paradigm is rarely an object for replication. Instead, like an
accepted judicial decision in the common law, it is an object for further articulation
and speculation under new or more stringent conditions.’

(10) As a source of tools (p. 37): ‘... the conceptual and instrumental tools the
paradigm supplies”

(11) Asa standard illustration (p. 43): ‘Close historical investigation of a given
speciality at a given time discloses a set of recurrent and quasi-standard illustrations
of various theories in their conceptual, observational, and instrumental applications.
These are the community’s paradigms, revealed in its textbooks, lectures, and
laboratory exercises. By studying them and by practising with them, the members
of the corresponding community learn their trade. The historian, of course, will
discover in addition a penumbral area occupied by achievements whose status is
still in doubt, but the core of solved problems and techniques will usually be clear,
Despite occasional ambiguities, the paradigms of a mature scientific community
can be determined with relative ease.’

(12) As a device, or type of instrumentation (pp. 59-60): ‘. . . they denied previously

64 MARGARET MASTERMAN

paradigmatic types of instrumentation their right to that title. In short, consciously
or not, the decision to employ a particular piece of apparatus and to use it in a
particular way carries an assumption that only certain sorts of circumstances will
arise. There are instrumental as well as theoretical expectations, and they have
often played a decisive role in scientific development. One such expectation is, for
example, part of the story of oxygen’s belated discovery. Using a standard test
for ‘‘the goodness of air”, both Priestley and Lavoisier mixed two volumes of their
gas with one volume of nitric oxide, shook the mixture over water, and measured
the volume of the gaseous residue. The previous experience from which this standard
procedure had evolved assured them that with atmospheric air the residue would
be one volume and that for any other gas (or for polluted air) it would be greater.
In the oxygen experiments both found a residue close to one volume and identified
the gas accordingly. Only much later and in part through an accident did Priestley
renounce the standard procedure and try mixing nitric oxide with his gas in other
proportions. He then found that with quadruple the volume of nitric oxide there
was almost no residue at all. His commitment to the original test procedure—a
procedure sanctioned by much previous experience—had been simultaneously a
commitment to the non-existence of gases that could behave as oxygen did. Illustra-
tions of this sort could be multiplied by reference, for example, to the belated
identification of uranium fission. One reason why that nuclear reaction proved
especially difficult to recognise was that men who knew what to expect when bom-
barding uranium chose chemical tests aimed mainly at elements from the upper end
of the periodic table. Ought we to conclude from the frequency with which such
instrumental commitments prove misleading that science should abandon standard
tests and standard instruments? That would result in an inconceivable method of
research, Paradigm procedures and applications are as necessary to science as
paradigm laws and theories... .’
(13) As.an anomalous. pack of cards.}
(14) As a machine-tool factory (p. 76): ‘So long as the tools a paradigm supplies
continue to prove capable of solving the problems it defines, science moves fastest
and penetrates most deeply through confident employment of those tools. The
reason is clear. As in manufacture so in science—retooling is an extravagance to be
reserved for the occasion that demands it.’
(15) As a gestalt figure which can be seen two ways (p. 85): ‘... the marks on
paper that were first seen as a bird are now seen as an antelope, or vice versa. That
parallel can be misleading. Scientists do not see something as something else;
instead, they simply see it. We have already examined some of the problems created
by saying that Priestley saw oxygen as dephlogisticated air. In addition, the scientist
does not preserve the gestalt subject’s freedom to switch back and forth between
ways of seeing. Nevertheless, the switch of gestalt, particularly because it is today
so familiar, is a useful elementary prototype for what occurs in full-scale paradigm
shift.’
(16) As a set of political institutions (p. 92): ‘. . . it is crisis alone that attenuates
the role of political institutions as we have already seen it attenuate the role of
paradigms.’
(17) As a ‘standard’ applied to quasi-metaphysics (p. 102): ‘And as the problems
change, so, often, does the standard that distinguishes a real scientific solution
from a mere metaphysical speculation, word game, or mathematical play.’

1Cf. Kuhn’s discussion of the Bruner-Postman experiment, op. cit. pp. 62-3.

THE NATURE OF A PARADIGM 65

(18) As an organizing principle which can govern perception itself (p, 112); ‘Sur-
veying the rich experimental literature from which these examples are drawn makes
one suspect that something like a paradigm is prerequisite to perception itself.’
(19) As a general epistemological viewpoint (p. 120): ‘... philosophical paradigm
initiated by Descartes and developed at the same time as Newtonian dynamics.’
(20) As a new way of seeing (p. 121): ‘Scientists... often speak of the “scales
falling from the eyes” or of the “lightning flash” that “inundates” a previously
obscure puzzle, enabling its components to be seen in a new way... .’

21) As something which defines a broad sweep of reality (p. 128): ‘Paradigms

etermine large areas of experience at the same time.’

It is evident that not all these senses of ‘paradigm’ are inconsistent with
one another: some may even be elucidations of others. Nevertheless, given
the diversity, it is obviously reasonable to ask: ‘Is there anything in common
between all these senses? Is there, philosophically speaking, anything
definite or general about the notion of a paradigm which Kuhn is trying to
make clear? Or is he just a historian-poet describing different happenings
which have occurred in the course of the history of science, and referring
to them all by using the same word “paradigm”’?”

Preliminary attempts to answer this query by textual criticism make
clear that Kuhn’s twenty-one senses of ‘paradigm’ fall into three main
groups. For when he equates ‘paradigm’ with a set of beliefs (p. 4), with a
myth (p. 2), with a successful metaphysical speculation (p. 17), with a.
standard (p. 102), with a new way of seeing (pp. 117-21), with an organizing
principle governing perception itself. (p. 120), with a map (p. 108), and
with something which determines a large area of reality (p. 128), it is
clearly a metaphysical 1 notion or entity, rather than a scientific one, which
he has in his mind. I shall therefore call paradigms of this philosophical
sort metaphysical paradigms, of. metaparadigms; and these are the only kind
of paradigm to which, to my knowledge, Kuhn’s philosophical critics have
referred. Kuhn’s second main sense é OF ‘paradigm’, however, which is given
by another group of uses, is a socialiiea sense. Thus he defines ‘paradigm’
as a universally recognized scientific achievement (p. x), as a concrete
scientific achievement (pp. 10-11), as like a set of political institutions
(p. 91), and as like also to an accepted judicial decision (p. 23). I shall call
paradigms of this sociological sort sociological paradigms. Finally, Kuhn
uses ‘paradigm’ in a more concrete way still, as an actual textbook or
classic work (p. 10), as supplying tools (pp. 37 and 76), as actual instru-
mentation (pp. 59 and 60); more linguistically, as a grammatical paradigm
(p. 23), illustratively, as an analogy (e.g. on p. 14); and more psychologi-
cally, as a gestalt-figure and as an anomalous pack of cards (pp. 63 and 85).
I shall call paradigms of this last sort artefact paradigms or construct
paradigms.

66 MARGARET MASTERMAN

From now on I shall assume (though with some apology to scholars) that
textual criticism of Kuhn gives us, in the end, only metaphysical paradigms,
sociological paradigms and construct paradigms; and I will discuss the
sociological sense of ‘paradigm’ first.

2. THE ORIGINALITY OF KUHN’S SOCIOLOGICAL NOTION OF A
PARADIGM: THE PARADIGM IS SOMETHING WHICH CAN FUNCTION
WHEN THE THEORY IS NOT THERE

Seen sociologically (as opposed to being seen philosophically) a paradigm
is a set of scientific-habits. By following these, successful problem-solving
can go on: thus they may be intellectual, verbal, behavioural, mechanical,
technological; any or all of these; it depends on the type of problem which
is being solved. The only explicit definition of a paradigm, in fact, which
Kuhn ever gives is in terms of these habits, though he lumps them all
together under the name of a concrete scientific achievement. ‘Normal
science’, he says (p. 10), means ‘research based upon one or more past
scientific achievements that some particular community acknowledges for
a time as supplying the foundation for its further practice’. These achieve-
ments are (i) ‘sufficiently unprecedented to attract an enduring group of
adherents away from competing modes of scientific activity’, and (ii)
‘sufficiently open-ended to leave all sorts of problems for the redefined
group of practitioners to solve. Achievements that share these two char-
acteristics I shall henceforward refer to as paradigms’. Thus, by assigning
the central place, in real science, to a concrete achievement rather than to
an abstract theory, Kuhn, alone among philosophers of science, puts him-
self in a position to dispel the worry which so besets the working scientist
confronted for the first time with professional philosophy-of-science,
‘How can I be using a theory which isn’t there?”

Kuhn himself has no doubt, moreover, that his paradigms, thus sociolo-
gically defined, are prior to theory. (This is part of the reason why he
wants a new word, other than ‘theory’ to describe them.) For ‘why’, he
asks himself (p. 11) is the paradigm, or scientific achievement, ‘as a locus of
professional commitment, prior to the various concepts, laws, theories and
points of view that may be abstracted from it?’ Unfortunately (and typi-
cally), having posed this highly germane question, Kuhn gives himself no
answer, and the reader is left to work out the answer for himself, if he can.
But at least it is made clear that, for Kuhn, something sociologically de-
scribable, and above all, concrete, already exists in actual science, at the
early stages, when the theory is not there.

It is worth remarking also that, whatever synonym-patterns Kuhn may
get trapped into establishing in the heat of his arguments, he never, in fact,

THE NATURE OF A PARADIGM 67

equates ‘paradigm’, in any of its main senses, with ‘scientific theory’. For
his metaparadigm is something far wider than, and ideologically prior to,
theory: i.e. a whole Weltanschauung. His sociological paradigm, as we have
seen, is also prior to theory, and other than theory, since it is something
concrete and observable: i.e. a set of habits. And his construct-paradigm
is less than a theory, since it can be something as little theoretic as a single
piece of apparatus: i.e. anything which can cause actual puzzle-solving to
occur, ;

Thus the widely-held popular views that Kuhn is not really saying any-
thing new: or that in so far as he is a philosopher at all, his views are
essentially the same as Feyerabend’s; or that he must be trying to say the
same things as Popper (since Popper first said everything that is true about
the philosophy of science), but that he does not say them very efficiently
or with the right kind of emphasis; all these judgements can be shown,
from actual examination of Kuhn’s text, to be false. It is, in fact, the very
differences between Kuhn’s ‘new image’ of science (or, as I shall from now
on call it, the ‘paradigm view’ of science) and all other philosophies of
science which are known to me, which is causing Kuhn’s book to be so
widely read, and which is prompting me to write the present paper.

I will therefore try to say, in the next section, what I think it is in
the paradigm view which, by successfully establishing the characteristic
scientificness of science, successfully combats the aetherial philosophicness
of the Popperian ‘falsifiable metaphysics’ view. After that I will try to say
something about the kind of effect that Kuhn’s paradigm view has on the
older and tighter ‘hypothetico-deductive view’ ; for the paradigm view sur-
prisingly seems to me to be much nearer to the second of these views than
to the first. In conclusion I will hint at what I think are going to turn out
to be the distinctive and revolutionary logical characteristics of Kuhn’s
paradigm, once it has been stripped of its sociological environment and
looked at generally and philosophically. I shall derive all these logical
characteristics from the paradigm’s basic property, which I shall call
concreteness or ‘crudeness’.

Before starting all this, and to round off this section, I will try to sketch
in, in an impressionistic manner, how I think Kuhn’s view of science
differs from Feyerabend’s, since Feyerabend is both the philosopher of
science who, so far, is nearest to Kuhn, and also the one who has given
Kuhn’s work most study.? The main difference, I think, is that, owing to
his general sociological bias, Kuhn’s interests are much more inclusive

1 T could document all of these; but I won’t.

2 Feyerabend [1962], p. 32. What is given here is a very cavalier account of Feyerabend's
paper, for which I ought to apologize, since I have given a positive and summary impression
of what is in fact a series of negative results.

68 MARGARET MASTERMAN

than Feyerabend’s. Kuhn is interested in both the rise and fall of science, in
the whole process of human beings trying to achieve a scientific explana-
tion. Feyerabend is interested only in the fall; all his analyses are about that
sense of explanation in which itis thought to be synonymous with reduction;
Feyerabend, for instance, presupposes at least one fully articulated theory
already to exist. But Kuhn does not presuppose anything; not even,
initially, his paradigms.! He researches into the real history, and broods;
he reads scientific teaching textbooks, and wonders. An investigation into
the originality of Kuhn, then, is also an investigation into the crude forms
and early stages of a science.

And this is, above all, what makes his work attractive to scientists in new
fields; pre-eminently, of course, to scientists in the social sciences, and in
experimental psychology. One of the reasons why professional philosophy
of science at present looks aethereal tq actual research scientists, is that
modern philosophers of science, taken as a group, have worked backwards.
First we had the hypothetico-deductive view, the datum of which is the
single, apparently all-inclusive, self-consistent, fully articulated, complete
and tight interpreted deductive system—that ideal which no science
reaches, but to which, if Kuhn is right, every teaching textbook, in an
advanced hard science, tries to approximate.? Subsequent to this, we have
had Feyerabend’s newer conception (following on Popper’s) of the stage
which comes before: that is, of two much younger, much less completely
finished-off theories which compete to cover what (though only in a Pick-
wickian sense) can be called ‘the same field’. No modern philosopher of
science has, as yet, gone back earlier; to the stages when there are either no
theories at all, as I am about to say in the next section, or far too many
theories (if the word ‘theory’ is used metaphysically or colloquially) and no
clear field. In view of the current proliferation of alleged new sciences,
however, it is overdue, if the philosophy of science is to become, as it
should, a scientifically useful guide to actual research workers, that some
informed philosophic move backwards should now be made.

Kuhn, in my view, has made this move; or tried to.

3. THE PHILOSOPHIC CONSEQUENCE OF KUHN’S INSISTENCE ON
THE CENTRALITY OF NORMAL SCIENCE: PHILOSOPHICALLY
SPEAKING, A PARADIGM IS AN ARTEFACT WHICH CAN BEUSEDASA
PUZZLE-SOLVING DEVICE; NOT A METAPHYSICAL WORLD-VIEW

It might be said, by those who are impressed by the analytic primacy
which Kuhn gives to sociology as opposed to philosophy, as giving the

1 Before he took up his present intellectual position, Kuhn’s development ranged over a
number of fields and went through at least six stages (see his [1962], preface pp. vii—x).
2 Kuhn [1962], p. 1; pp. 1-2; p. 10; pp. 135 ff.; p. xi; and see also section IV, below.

THE NATURE OF A PARADIGM 69

main clues to the foundations of real science, ‘Why do you flog this notion
of “paradigm” any further? It’s just Kuhn’s name for a set of habits, that’s
all. These exist, granted; but the fact is of no philosophical importance.’

This is not correct, even about Kuhn. Besides his sociological paradigms
(sense 2), he has metaphysical paradigms (sense 1), and also artefact
paradigms, or construct paradigms (sense 3). It is easy to show that he has
at least these. But quite apart from what Kuhn, taken now as a philosopher,
has actually said about paradigms, there is a deeper and more immediate
reason for not being satisfied with a purely sociological sense of ‘paradigm’,
which is that any definition of this is bound to be circular, For, to estab-
lish the paradigm’s (temporal) priority to theory in scientific action, we
have to define it, sociologically, as an already known concrete scientific
achievement, an already established set of habits. But how does the scientist
himself, in a new science, first find out that what he is following is going to
become a concrete scientific achievement, unless he already knows that he
is following a paradigm? There is clearly a circularity here: first we define
a paradigm as an already finished achievement; and then, from another
point of view, describe the achievement as building up round some al-
ready existent paradigm.

It could be argued, of course, that if we seriously undertook the detailed
sociology, obtained by observation, of fresh contemporary new sciences,
instead of confining ourselves to the detailed history, obtained through
hindsight, of stale past sciences, this circularity, for practical purposes,
could be broken down; since if they existed, we could then detect para-
digms in the process of being formed. But even then, how would we know
that it was paradigms which we were looking for, as opposed to other
things, unless we already knew, non-sociologically, what a paradigm was?
The primary sense of ‘paradigm’, clearly, has got to be a philosophic one;
and the paradigm has got to exist prior to the theory. This once estab-
lished, the man who says, ‘What, in actual fact, is this “‘paradigm’’, this
entity?’, can then indeed be answered by being told to go and look at what
is happening in a new scientific field. For in a new science, not only is the
formal theory almost sure to be missing; but also a very great deal of high-
powered scientific activity is aimed at the right choice of the moment when
it will be worth the labour to construct it. The alternative is ‘just going on
as we are now’; that is, with some trick, or embryonic technique, or picture,
and an insight that this is applicable in this field. And it is this trick, plus this
insight, which together constitute the paradigm. The explicit metaphysics
(what the scientist himself calls ‘the philosophy’ or ‘the gas’), the fuller
mathematicizing innovation, the more developed experimental procedures
—all those things which, taken together, will later become ‘the concrete

70 MARGARET MASTERMAN

established scientific achievement’—nearly always come long after the initial
practical trick-which-works-sufficiently-for-the-choice-of-it-to-embody-a-
potential-insight, that is, after the first tryout of the paradigm. In fact,
and in genuine and live science, the very effort to establish a ‘concrete
scientific achievement’ has to justify itself. For the resultant theory (and/or
the more exact and expensive technique) to be acceptable, it must enable
results to be obtained which could not be obtained otherwise. No good
scientist wants to establish such an achievement just to figure later in books
on the philosophy of science. Still less does he want theoretically to clean
up his subject at the cost of removing from the hitherto used colloquial
description of the facts any possible analysis of the real centres of difficulty.
Thus the real problem, in getting a philosophy of new science, is to de-
scribe philosophically the original trick, or device, on which the socio-
logical paradigm (i.e. the set of habits) is itself founded.

With all this in mind, it is enlightening to turn again comparatively to
Kuhn’s first and third senses of ‘paradigm’. As has been seen, if we ask
what a Kuhnian paradigm is, Kuhn’s habit of multiple definition poses a
problem. If we ask, however, what a paradigm does, it becomes clear at
once (assuming always the existence of normal science) that the construct
sense of ‘paradigm’, and not the metaphysical sense or metaparadigm, is
the fundamental one. For only with an artefact can you solve puzzles. And
though, having initially asserted (p. 36) that he is going to use ‘puzzle’ in
the literal, standard, dictionary sense, Kuhn later weakens and talks (p. 42)
about ‘the metaphor that relates normal science to puzzle-solving’, yet, in
general, he has a steady, literal and very concrete idea of what he means by
the puzzle-solving activity of normal science. A normal-scientific puzzle
always has a solution (p. 36) which is guaranteed by the paradigm, but
which it takes ingenuity and resourcefulness to find. Typically (p. 35), the
solution is known beforehand, as with any other puzzle, but the step-by-
step route to it is not. The normal scientist is a puzzle-solving addict
(p. 37); it is in this puzzle-solving —not just vague ‘problem-solving’, but
puzzle-solving—that normal science prototypically consists. And a puzzle
is always an artefact. It is all very well to say that the paradigm ‘supplies
tools’ (pp. 37 and 76) or, vaguely, that it makes problem-solving possible.
It remains true that for any puzzle which is really a puzzle to be solved by
using a paradigm, this paradigm must be a construct, an artefact, a system,
a tool; together with the manual of instructions for using it successfully and
a method of interpretation of what it does.

However, if it is true that it is Kuhn’s construct-paradigm, and not either
of his two other main senses of ‘paradigm’, which provides the philosophical
clue to what paradigms in a new science really are, by pinpointing the trick

THE NATURE OF A PARADIGM 71

or device which starts off a new science; if all this, then why is it that
all philosophers of science other than myself have thought it evident
that by ‘paradigm’ Kuhn meant a metaphysical world-view, that his
primary sense of ‘paradigm’ was sense I, not sense 3? The immediate
explanation of this is easy. They did not take Kuhn’s account of normal
science seriously. However, it might still be thought that by saying all this
I intend to repudiate all that philosophers of science are currently saying
about science emerging out of metaphysics (the ‘falsifiable metaphysics’
view); or that I am ignoring what Kuhn himself says about preparadigm
science?; or that I am laying down the law in a Marxist manner about the
motivation for all new science being technological. This is not so. It is
obvious that one of the roots of scientific achievement is metaphysical, as
Popper, Kuhn himself and many others have said, But the current philoso-
phic bias has gone so much towards examining what is conceptual, in
thinking about the nature of any science, that philosophers have all but
forgotten to allow for what is practical. Thus Kuhn has not seen the
relevance, in discussing the verification problem, of final technological
application?; and Popper has not seen the relevance, in discussing the
emergence of science out of metaphysics and philosophy, of the technical
trick which starts off each new science. Though he must have heard the
old saw to the effect that science is a marriage between metaphysics and
technology, Popper never asks himself how the copulation occurs; conse-
quently, the fatal weakness of the Popperian view of science is that the
Popperians can provide no answer to the question, ‘If a scientific system is
essentially a metaphysical system which is falsifiable, how can the meta-
physics itself be used as a model, and subjected to test?’.

This brings me to my promised comparison of Kuhn and Popper; or,
more exactly, to a comparison between the paradigm view of new science,
and the Popperian view. For the gross lacuna which I assert to be in the
Popperian view—namely, that Popper cannot account for how any new
research line suddenly starts up—this is not due, as is sometimes alleged
by cynics, to the fact that Popperian philosophers of science are incapable
of understanding technology, or that technologists are incapable of thinking
Popperianwise about the philosophy of science. Neither of these assertions
is true, and both are irrelevant. What has caused the trouble, in my judge-
ment, is excessive reliance upon Newton. Newtonian mechanics, just
because it has lasted so long, is in the unique position, among scientific

1 And indeed I am being cavalier about what Kuhn says about preparadigm science;
just as I was earlier cavalier about Feyerabend. See, however, the discussion of it at the
end of this section.

2 Kuhn [1962], pp. xii, 19, 69 and 166-7; Kuhn thinks technology is outside the sphere
of the philosophy of science.

72 MARGARET MASTERMAN

theories, of being able to be regarded either as quasi-metaphysics, or as the
very prototype of deductive theory, or (now) as technology, according to
how you choose to look at it. Moreover, reliance upon Newtonian mech-
anics, as being always there to be ambiguously pointed at in any crisis as
to what science is, is slavish. If all the philosophers of science who derive
from Kant had not been able to equate science with Newtonian mechanics,
where would the philosophy of science be? Popper himself, indeed, in
Conjectures and Refutations, sees one great difficulty in making this equa-
tion; but whereas Popper thinks that the trouble lies (for us, but not for
Kant) in the fact that we must now consider Newton’s theory ‘as a hypo-
thesis whose truth is problematic’ since ‘Einstein has shown that it is
possible, using basic principles very far removed from those of Newton,
to do justice to the entire range of the data of experience’, in fact the
trouble with Newtonian mechanics is that it works so completely that it
has now become part of technology, namely the technology of sending up
space satellites. On Kuhnian principles, therefore, and I think also on
Popper’s, it is no longer part of the philosophy of science.

Self-deprived of Newton, Popper thenceforward makes a very much
poorer show of giving a realistic account of creative thinking in science.
‘We invent our myths and our theories and we try them out’, he says*—to
which the answer is: ‘How?’ ‘When?’ ‘Where?’ Theories ‘are seen to be the
free creations of our minds’, he continues, ‘the result of an almost poetic
intuition’*—to which the short answer is: ‘Who so sees them?’ ‘We do
not try to prove them... but...to refute them’*—to which the only
answer is: ‘In fact, do we?’ At the earliest opportunity, moreover, Popper
leaves discussion of scientific theories altogether to turn to philosophic
theories, in order to analyse, brilliantly, whether these are not also, in a
more direct way, refutable. He then, bar a hairsbreadth, equates these with
scientific theories®; and one suspects that—apart from Newton—it is
these, and not science as it really is, which he has had at the back of his
mind all the time.

It is this virtual equation (bar Newton) of scientific thinking with specu-
lative philosophical thinking which, more than any one other thing, cur-
rently gives rise to what I described at the beginning as ‘philosophy-of
science aetherialism’. By contrast with this abstractness, Kuhn, by in-
sisting on the sociological importance of the actual set of habits which, in
fact, characterize any new science, and which are prior to any formulation
of theory, has succeeded in establishing, as central to his philosophy, the
essential concreteness which is characteristic of science; i.e. in remaking

2 Popper [1963], p. 191. ? Popper [1963], p 192. 3 Loc. cit.
* Loe. cit. ‘ ® Popper [1963], pp. 199-200.

THE NATURE OF A PARADIGM 73

the distinction which the scientist himself in his talk makes between the
actual ‘picture’, or the ‘model’, and the ‘philosophy’. This ‘model’ (the
operation of which I have described earlier as the trick, or device, which
starts off any new science or research line) becomes for Kuhn his construct-
paradigm (paradigm sense 3), the use of which enables the puzzle-solving
of normal science to be performed. And it is this identification in its turn—
ie. the fact that it is the construct-sense of paradigm and not the meta-
physical sense of paradigm which has to be Kuhn’s primary sense of
paradigm—which enables him then to make a new interrelation between
model-using and metaphysics. For instead of asking ‘How is it that a
metaphysical system can be used as a model?’—i.e. instead of asking the
question which I said earlier that the Popperians could not answer—Kuhn
can now ask: ‘How is it that a puzzle-solving construct (i.e. a paradigm,
sense 3) can be used metaphysically? How, in fact, can a construct-paradigm
become a ‘“‘way of seeing’’?’

Consideration of this question forces us sharply back from the Popperian
impression of science in general to a more sophisticated re-evaluation of
the hypothetico-deductive conception of the exact function of a scientific
theory. For, after all, an hypothetico-deductive system—if it can be con-
structed at all—is, by its nature, a problem-solving artefact. Before we go
on to this, though, there is one confusion to clear up; which is what Kuhn
himself says about the nature of new, or first stage, or preparadigm,
science. For I said earlier that a consideration of the originality of Kuhn
was also an investigation into the crude origins, and early stages, of any
science; and I confirmed this by advancing reasons for thinking—as well
as by showing that Kuhn thinks—that paradigms already exist when the
theory is not there. But this immediately prompts the further question:
‘What does Kuhn think exists, then, even before the paradigm?”

This is one of the points on which I disagree with Kuhn, in that his
general view of the preparadigm science seems to me both confused and
incompletely analysed. As I see it, he fails to distinguish from one another
three relevant states of affairs, which I will call respectively non-paradigm
science, multiple-paradigm science, and dual-paradigm science. Non-paradigm
science is the state of affairs right at the beginning of the process of thinking
about any aspect of the world, i.e. at the stage when there is no paradigm.
Of this state Kuhn says (p. 15) that in it only the easily accessible facts are
collected, and these in a casual manner, unless some more recondite facts
have been made available by technology; that this is because, at this stage,
all facts seem equally relevant; and that different but overlapping sets of
facts are interpreted in differing metaphysical or quasi-fanciful ways. He
further says (p. 11) that ‘there can be a sort of scientific research without

74 MARGARET MASTERMAN

paradigms ...’, but that it is non-esoteric; and (pp. 13, 100 and 163) that
in such research ‘though the field’s practitioners were scientists, the net
result of their activity was something less than science’. He further notes
(p. 20) that in such situations the book (as opposed to the article) possesses
‘the same relation to professional achievement that it still retains in other
creative fields’; that every individual scientist starts over again from the
beginning (p. 13); that there are a number of competing schools directing
their publications primarily against one another (p. 25); that there is con-
tinual philosophic discussion over fundamentals (p. 159); and no progress
(pp. 159 and 163). In short, non-paradigm science is barely distinguishable,
if at all, from ‘the philosophy of’ the relevant subject, and is covered by
Popperian analysis.

This pre-scientific and philosophic state of affairs sharply contrasts,
however, with multiple-paradigm science, with that state of affairs in which,
far from there being no paradigm, there are on the contrary too many.
(This is the present overall situation in the psychological, social and infor-
mation sciences.) Here, within the sub-field defined by each paradigmatic
technique, technology can sometimes become quite advanced, and normal
research puzzle-solving can progress, But each sub-field as defined by
its technique is so obviously more trivial and narrow than the field as
defined by intuition, and also the various operational definitions given by
the techniques are so grossly discordant with one another, that discussion
on fundamentals remains, and long-run progress (as opposed to local
progress) fails to occur. This state of affairs is brought to an end when
someone invents a deeper, though cruder (p. 23) paradigm, which gives a
more central insight into the nature of the field, though restricting it and
making research into it more rigid, esotoric, precise (pp. 18 and 37). This
(p. 16) either by causing rival, more shallow paradigms to collapse, or
alternatively, by attaching them somehow or other to itself, triumphs over
the rest, so that advanced scientific work can set in, with only one total
paradigm. Thus multiple-paradigm science is full science, on Kuhn’s own
criteria; with the proviso that these criteria have to be applied by treating
each sub-field as a separate field.

During the period of crisis, however, just before a scientific revolution,
Kuhn says (pp. 84 and 86) that many of the characteristics of pre-paradigm
science again set in, ‘except that the locus of difference [between the
competing schools] is both smaller and more defined’. During this period
there are always two competing paradigms struggling for the mastery
(pp. 75 and 91); I have therefore described it as dual-paradigm science.

The reason that Kuhn fails sufficiently to distinguish non-paradigm
science from multiple-paradigm science, and therefore sufficiently to

THE NATURE OF A PARADIGM 75

connect multiple-paradigm science with dual-paradigm science, is due
partly to a confusion; having said that there can be a sort of scientific
research without paradigms, he then adds, ‘or at least without any so
unequivocal and binding as the ones named above’ (p. 11), as though
these two states of affairs were identical. It is also partly due to the insuffi-
cient place within science which he gives to technology, which exists plenti-
fully and sometimes excessively in multiple-paradigm science, but only
non-relevantly, if at all, in non-paradigm science.

As opposed to this complicated and confused preparadigm survey of
Kuhn’s (and taking his notion of ‘normal science’ seriously) I have simplified
the position by saying squarely that when ‘normal science’ sets in, anywhere,
there you have science, and where it does not set in, there you have philo-
sophy or something else, not science, and that it is always some construct-
using, puzzle-solving trick which starts off normal science. This assertion
exposes me to attack in two ways. Firstly I can be attacked for not being
able to distinguish a single new research line from a total new science (see,
for instance, the passage earlier where I equated the two with one another),
and therefore in the terminology just given above, of not being able to
distinguish multiple-paradigm science from mature single paradigm science.
This attack is correct. In my view the two can only be distinguished from
one another later, by hindsight, when a total new science with one vast
paradigm, is ultimately seen to have been created through the convergence
of a number of paradigm-guided research lines which mutually threw light
on one another. The second attack which can be made on me is that if I
distinguish ‘science’ from ‘philosophy’ only because within science there
always somewhere occurs normal science, what about the converse case
where ‘normal science’ prematurely sets in in some unjustified manner, by
a set of fashion-following scientists starting to imitate one another without
proper pre-examination of the paradigm (i.e. without the alleged insight
that a certain paradigm is relevant to a particular field being a genuine
insight)? My reply to this is: ‘What indeed?’ Do we not see premature
‘normal science’ (which is also called ‘phoney science’ and ‘pseudo-
science’ by soured critics) setting in all round us in a nightmarish manner,
in the newer sciences, especially where computers can be grandiosely used
to give a spurious impression of genuine scientific efficiency? But the fact
that new science can be exceedingly bad does not cause it to cease to be bad
science (as opposed to bad philosophy, bad painting or other bad what-
have-you). In the end phoney scientific normal-research lines collapse, or
fail to yield any results, or topple, or evaporate—or so one hopes; and so
in the past (e.g. in the case of astrology which, as Watkins says, was in
some ways exceedingly ‘normal’) it has finally proved.

76 MARGARET MASTERMAN

Having done what can be done to establish non-sociologically a Kuhnian
paradigm as a genuinely insightful puzzle-solving trick or device, let us
now both examine further the nature of the device, and also, if possible,
the nature of the insight.

4. A PARADIGM HAS GOT TO BE A CONCRETE ‘PICTURE’ USED ANALO-
GICALLY ; BECAUSEIT HASGOTTOBEA ‘WAY OF SEEING’

If a paradigm were only to be an interpretable construct or artefact the
use of which had become an established social institution, it might be hard
to distinguish Kuhn’s paradigm view of science from some sociologically
sophisticated hypothetico-deductive view; all the more so, as I think it can
be shown that Kuhn’s paradigm-view of science has a little more in common
with the hypothetico-deductive view than a superficial reading of his book
would imply. For in spite of his apparently vague and poetic style, both
he and the hypothetico-deductivists are struggling to say something about
the development of science which is exact. What distinguishes the two
views from one another is that a puzzle-solving paradigm, unlike a puzzle-
solving hypothetico-deductive system, has also got to be a concrete ‘way
of seeing’.

With hypothetico-deductive system-making in mind, let us see what
Kuhn does say. He repeatedly compares the switch from one scientific
paradigm to another to the operation of ‘re-seeing’ an ambiguous gestalt-
figure! or to being subjected to a gestalt-psychological experiment.? Note
therefore that each of these is a completely specifiable artefact which has
been specially constructed to be itself a ‘way of seeing’; in fact, to be two
alternative ways of seeing. When, however, we compare the paradigm
itself to a gestalt-figure, the comparison becomes trivial; because if, to do
so, we now ask ourselves what a gestalt-figure is like when it represents
only one way of seeing, we get the trivial answer that it is a perfectly
ordinary picture of a simple concrete object. Moreover, the gestalt-figure
comparison fails also in yet another respect, in that an ambiguous gestalt-
figure, unlike a paradigm, cannot be extended or developed, since any
extra detail which is added will be bound to bias it either towards one of
its interpretations, or towards the other.®

What Kuhn must be feeling his way to, in talking about an artefact
which is also a ‘way of seeing’, is an assertion, not about the nature of his
artefact, but about its use: namely, that being a picture of one thing, it is

1 Kuhn [1962], pp. 85, 110, 113, 116, 119, 121, 125 and 149,

2 Ibid. pp. 62, 64, 111, 112 and 125.

3 ‘This can be seen particularly clearly from examination of the perceptually ambiguous
gestalt-figures in Gregory [1966].

THE NATURE OF A PARADIGM 77

used to represent another—for example, the geometrical model made of
wire and beads, though it is primarily a glorification of a well-known kind
of child’s toy, is used in science to represent a protein molecule.

It is, in fact, actual artefacts used analogically which Kuhn is after, as
have been many other philosophers of science from Norman Campbell to
Hesse. But Kuhn’s artefact, unlike Hesse’s,! cannot be a simple four-point
analogy or a material analogy, because it has got to be an organized puzzle-
solving gestalt which is itself a ‘picture’ of something, A, if it is then to be
applied, non-obviously, to provide a new ‘way of seeing’ something else, B.

Unlike Kuhn’s two-way gestalt-figure, however, his paradigm does not
itself have to be ambiguous as well as non-obvious in its application; it can,
therefore, with caution, be developed, like other analogies. The question
sharply arises, though: how is it to be developed? And is there any real
sense in which an analogy, as contrasted with a model or a mathematical
system, can be an artefact?

Before, in conclusion, we discuss this, more must be said of how Kuhn’s
paradigm is to be distinguished from a scientific hypothetico-deductive
theory by the fact that it is a ‘way of seeing’. To say that it is a concrete
constructed ‘picture’ or device used analogically is not enough. For, it
could be replied, a mathematical system itself, and even when uninter-
preted, is, notoriously, a very abstract ‘way of seeing’. For the man using
it can always be asked, particularly in a new science, for example, “Why
are you using zhat mathematical system, and no other?’, or, ‘Are you sure
that this mathematical picture which you are building up is giving you the
kind of space which you will later want when your experimental evidence
has been organized more sharply?’ Moreover, according to the hypothetico-
deductive view, the mathematics used in science are not uninterpreted.
They are coloured—‘faintly tinted’, would be a better description, for the
colouring-mechanism is never sufficiently made clear—by the still more
highly coloured concrete truths which form the lower, more particular
parts of the system. On this view, concreteness and interpretation are sup-
posed to seep back and up, somehow, from the more concrete lower parts
to the more abstract and aethereal higher parts; thus making of the whole
hypothetico-deductive edifice an artefact which could indeed be held to be
a ‘way of seeing’, par excellence.

Kuhn’s paradigm’s ‘way of seeing’, however, really is different from
this—and not only because, as asserted earlier, his paradigm already exists
when the theory is not there. It is different because his paradigm is a con-
crete ‘picture’ of something, A, which is used analogically to describe-a
concrete something else, B. (That is, the trick which, as I said earlier,

1 Hesse [1963], pp- 70-3.

78 MARGARET MASTERMAN

starts off every new science, is that a known construct, an artefact, becomes
a ‘research vehicle’, and at the same moment, if successful, it becomes a
paradigm, by being used to apply to new material, and in a non-obvious
way.) It thus has two kinds of concreteness, not one: the concreteness
which it brought with it through being a ‘picture’ of A, and the second
concreteness which it has now acquired, through becoming applied to B. This
second kind of concreteness is the kind which the hypothetico-deductive
view of science tries to account for; but the first, on the hypothetico-
deductive view, is not accounted for at all. If, however, we complicate the
hypothetico-deductive view by saying, as Campbell, in effect, does,! but
Hesse, I think, does not,? that there is always an analogy or a concrete
model at the heart of any mathematics used in science, and that this model
is not merely something attached afterwards, to be used heuristically or as a
mechanical aid; if we say further, as indeed Campbell more than once does
say, that it is this analogy which guides and restricts the theory’s articula-
tion, excising and removing, by the need to preserve it, the otherwise
excessive possibilities of abstract development inherent in all mathematics,
then the first kind of concreteness (call this A-concreteness) is accounted
for as well as the second kind (call this B-concreteness). For A-concrete-
ness now becomes the concreteness which the analogy brings with it to the
mathematics from the time before it was an analogy, when it was only a
‘picture’ of A; whereas B-concreteness is what seeps back into the mathe-
matics from the field of application, B. The abstract entities in the result-
ing theory can then be doubly interpreted—as indeed in a new science
they have to be—firstly A-wise, in terms of the generating analogy, and
secondly B-wise (that is, operationally, and, as the theory develops, in-
creasingly) in terms of data taken from the field to which the theory is
being applied.

That there are, quite obviously and in fact, A-components as well as
B-components in scientific theories, will be seen at once as soon as philo-
sophers of science start looking around them at fresh science instead of
looking only backwards at stale science, or alternatively, and in a self-obfus-
cating attempt to be up-to-date, goggling only from afar at the increasing
variegation of chaos in theoretic quantum mechanics. The most striking
example I know of the distinction is given by the Genetic Code. Here the

1 Campbell [1920]; see especially, pp. 129-30.

2 Hesse’s mind is split on the question as to whether analogy is at the heart of theory, as
Campbell says, or only an aid to it. In her [1963] she argues brilliantly, in effect, for a
Campbellian view; but in her [1964] she says only that ‘the deductive model of scientific
explanation should be modified and supplemented by a view of theoretical explanation as
metaphoric redescription of the domain of the explanandum’ (p. 1), thus still putting the
mathematical cart before the metaphorical horse.

THE NATURE OF A PARADIGM 79

initial A-concreteness is given by a ‘picture’ of language, which has now
been extended to include not only ‘letters’ and ‘words’, but also ‘sentences’
and ‘punctuation’; whereas the operational B-reinterpretation in terms of
operational procedures is biochemical.

I will take it from now on that I have established that there are two
operational components, the A-component and the B-component, even in
an idealized scientific theory; and that, whereas the hypothetico-deductive
view only allows for the second, Kuhn’s paradigm-view stresses the first.
Both have to be distinguished, in behaviour, from their common mathe-
matical clothing: further considerations which assist in making this dis-
tinction are given in conclusion below. Enough has been said, however,
to give the case for saying that, within the current scope of the philosophy
of science, the primary enterprise, in discovering the philosophical nature
of a Kuhnian paradigm, now becomes that of prising out the A-component
of a developed theory, the paradigm, from its also B-interpretable mathe-
matical envelope.?

5. CONCLUSION: PREVIEW OF THE LOGICAL CHARACTERISTICS OF
A PARADIGM

If a paradigm has got to have the property of concreteness, or ‘crudeness’,
this means that it must either be, literally, a model; or, literally, a picture;
or, literally, an analogy-drawing sequence of word-uses in natural language;
or, some combination of these.

In any of these cases, I wish to say that a paradigm draws a ‘crude
analogy’; and further to define a crude analogy as an analogy which has the
following logical characteristics:

(a) a crude analogy is finite in extensibility

(b) it is incomparable with any other crude analegy

(c) it is extensible only by an inferential process of ‘replication’, which can
be examined by using the computer-programming technique of
‘inexact matching’, but not by the normal methods of examining
inference.

The problem of saying something philosophical and yet exact about such
a paradigm (which now becomes that of saying something general and
exact about the nature and methods of operation of a concrete artefact,
constructed of pigments, or wire, or language) cannot be attacked within
the confines of this paper ; all the more so as it is, I think, the same problem

1 It is worth remarking that, on this view, the domain of the philosophical paradigm,
or crude paradigm, is narrower by far than that of the sociological paradigm, or total
paradigm, seen historically and by hindsight. For this second includes within itself every-
thing the operation of which could become a habit; including, ideally, the mathematical
part and the B-experimentation of an hypothetico-deductive system.

80 MARGARET MASTERMAN

which Black tries to attack when he tries to discover the nature of an arche-
type,! or when he asks himself how he is going to formalize the ‘inter-
action view’ of metaphor used in language.? In my view, the new ‘way of
seeing’ produced by Black’s metaphoric ‘interaction’ is an alternative form
of that produced by Kuhn’s gestalt-switch.

Here, I will only point out, in conclusion, that once the concreteness,
or ‘crudeness’ of an initial paradigm is granted, then great simplification
can be achieved in several areas of the philosophy of science. For instance,
when Kuhn says that his paradigms are not directly comparable with one
another, his word for this is ‘incommensurable’, and the context makes
clear that he is thinking of advanced science. But if one tries to construct a
general and exact notion of this incommensurability, as Feyerabend does,
then it can be shown, I think, that the attempt leads to great philosophic
difficulties, as well as producing a reductio ad absurdum of real science. And
if we merely envisage a concrete paradigm which draws a crude analogy,
then, notoriously, in so far as it is really crude, it will not be directly com-
parable with any other crude analogy. (How, for instance, can you compare,
‘Man, the paragon of animals’, to ‘Man, that wolf’?) Note also that this
agreed non-comparability depends on the crudeness. It does not hold when
the paradigm in question has become embedded in mathematical form,
except in so far as it is the A-component and not the B-component which
is in question. For the A-component, being concrete, draws a crude
analogy; whereas the B-component, being mathematical-cum-operational,
draws, if any analogy, only a mathematical analogy; and analogies between
pieces of mathematics render them not incommensurable, but conversely,
comparable.

The property of crudeness allows a comparable simplification to be made
of Kuhn’s statements to the effect that a paradigm must be finite in extensi-
bility. For in so far as the crude analogy drawn by a paradigm is not merely
like that drawn by a speaker in natural language but is one, then it is
notorious that it cannot be developed too far (all poets know this); whereas,
by contrast, mathematical extensibility is always imagined as being capable
of going on and on by accretion, indefinitely.

In this matter I have to confess that (inspired by Feyerabend) I also
was not content with the simplification produced by the postulate of
paradigm-crudeness, but tried to construct an abstract general notion of
non-extensibility. I started with the logicians’ traditional generalizing
device of analogy—as expounded, say by Jevons*—and then tried to prove

1 Black [1962], chapter xiii.

2 Ibid, chapter iii.

3 Jevons [1873]: see Analogy in the index; and also chapter ii, on the logic of terms, and
especially pp. 25-7.

THE NATURE OF A PARADIGM 81

finiteness in extensibility by using the logic of terms. To do this requires
saying that the kind of analogy we want, i.e. one which makes the applica-
tion of a whole A-organization to a B-field, counts as an instance of the
qualification by a complex ‘adjective’ of a general name, or ‘noun’. If we
could allow this, we could then say that the intension-extension law of the
logic of terms would apply also to this case, in the form that when the
meaning-in-extension of such an ‘adjective-noun’ is indefinitely increased
by the addition of further ‘adjectives’, its meaning-in-extension is corres-
pondingly decreased. Thus, no matter what threshold or zero limit of
intelligible meaning one sets up, there comes a stage when the continually
extending sequence goes over it; thereby exhibiting the phenomenon of
‘death by a thousand qualifications’. But I do not think that the develop-
ment of the paradigm-analogy which is made when a good new scientific
research line is started, can count as a straight-forward extra term-quali-
fication, since the whole point of it is that it causes new features of the
field of application to be discovered which would never have been noticed
without the help of the paradigmatic analogy, thus increasing the meaning-
in-extension of the whole term-sequence by adding to that which it
denotes, i.e. to the field.

So, my attempt to be abstract about paradigm-extensibility failed, and I
found myself left with the inescapable property of crudeness, trying to
explain ignotum per ignotius; i.e. of explaining a logically unknown entity, a
paradigm, by means of an even more unknown logical property, crudeness.
The heart of the problem is that of envisaging a crude analogy stated in
ambiguous words as an artefact; pictures and wire models can be fitted in
with comparative ease, after this first central problem has been faced. And
faced it must be; because, if what the scientist working in a new science is
actually doing is constructing and extending a crude analogy by using
speech, with or without the help of mechanical apparatus or of mathe-
matics, then the evident fact that natural language is continually used by
scientists, and sometimes to draw crude analogies with, this skeleton, has
got to come out of the philosophico-logical cupboard. This is especially so
as an increasing number of papers in the literature now discuss ‘semantics’
or ‘meanings’ within science, and, through absence of explicit confronta-
tion with the problem of word ambiguity, say some very extraordinary

things about it indeed.

1 See not only Feyerabend’s [1962] but also Brodbeck [1962] and Putnam [1962]; and the
earlier Ryle-Toulmin-Scriven bibliography that they refer to.

Of these, Feyerabend’s error seems to me to be philosophic: fulminating indiscriminately
against linguistic philosophers, he fails to distinguish the truisms of natural language from
the combinatorial resources of natural language. Brodbeck makes statements to the effect
that physicists’ colloquial conversation is elliptical, allusive and laconic, as well as context-
bound, whereas their official reports are explicit, comprehensible, logically complete, and

82 MARGARET MASTERMAN

Kuhn’s own account of the limits and extensibility of a paradigm is both
sketchy and faulty, for which fact he himself apologizes.‘ On the other hand,
the way in which he describes a paradigm breaking down, by the emer-
gence within it of anomaly which deepens into crisis, is at once illuminating
and realistic, when applied to a new science. His essential point is that an
anomaly is an untruth, or a should-be-soluble-but-is-insoluble problem, or
a germane but unwelcome result, or a contradiction, or an absurdity, which
is thrown up by the paradigm itself being pushed too far*; not just an inci-
dental counter-argument to the theory, or an awkward fact, which Kuhn
correctly characterizes as merely an ‘irritant’? Neither is it an extra-
paradigmatic novelty,* nor a problem which used to exist within the field
at an earlier stage, but which the developers of the paradigm have now
suppressed and rendered invisible, because it is incompatible with the
paradigm’s ‘basic commitment’.> The anomaly, to be a true anomaly, has

context-free; or at least when they are not, it is because they fail to approximate to an ideal
Platonic Physicist’s Report which they might have written but did not (pp. 237-8). She
also makes unsophisticated remarks of the kind that the ordinary-language philosophers
have correctly criticized, e.g. to the effect that, ‘it is necessary that white horses are white’,
is a statement from normal English Prose, whereas, in fact, it is either an obvious example
from a logic-book, or an untrue but rather splendid poetic remark which might refer to
waves, pubs, favourite writers, and angelic transport, as well as to natural animals (p. 238).
She further asserts that logicians’ language is useful to the philosopher ‘precisely because
and only in so far as it is a reconstruction of a large part of the language that we speak’
(ibid.). Putnam profoundly wrestles with Quine’s ‘All bachelors are unmarried’; but in
the course of doing so asserts not only that ‘bachelor’ is context-free (thus forgetting
bachelor’s buttons, bachelors of arts, medieval knights’ assistants—and Fodor and Katz);
but also that it is not law-clustered (forgetting equally the effect on the use of the word
‘male’ of testerone experiments and chromosome-aberrancies of intersexes), Likewise—
though in an exceedingly interesting article—he commits himself to the rash statement
(p. 362) that there areno synonymies and analyticities underlying language (after all, Strawson
might be right); and to the false statement that linguists know how to describe a natural
language in terms of a set of rules (pp. 389-90).

Clearly, when exceptional thinkers make remarks like these, a new kind of insight is
needed on the whole subject.

1 Kuhn [1962], pp. 86 and 89. At only one point does Kuhn argue that paradigms must
be non-extensible (on pp. 95-6); mostly he just retreats into history, and says that they are.

2 Kuhn [1962], p. 65 (see also, pp. 5, 52 and 78).

3 Kuhn [1962], pp. 78-9. Kuhn’s actual phrase (on p. 78, line 12) is ‘minor irritant’.

4 See above, footnote 2; especially p. 5, on the suppression of fundamental novelty;
and all other passages which would be listed under ‘novelty’ in a Kuhn index if there were
a Kuhn index. See also, in the same imagined index, ‘anomaly’.

5 Kuhn [1962]: p. 5 again (for the notion of ‘basic commitment’); p. 102, ‘. . . the recep-
tion of a new paradigm often necessitates a redefinition of the corresponding science. Some
old problems may be relegated to another science or declared entirely ‘“‘unscientific” ’;
p. 37, ‘... one of the things a scientific community acquires with a paradigm is a criterion
for choosing problems that, while the paradigm is taken for granted, can be assumed to
have solutions. To a great extent these are the only problems that the community will admit
as scientific or encourage its members to undertake. Other problems, including many that

THE NATURE OF A PARADIGM 83

got to be produced from within the paradigm. So that, if the paradigm is
to be conceived as a crude analogy, the anomaly, in its simplest and
crudest form, will correspond to Hesse’s neutral analogy which turns out
to be negative analogy}; i.e. to a set of statements (or laws) developed from
within the analogy itself, which should have been true, had the analogy
held that far, but which, since the analogy does not hold that far, turn
out to be false. In this simple situation, attempts will inevitably be made to
adjust the analogy; in the more complex, mathematicized situation,
attempts are made either to derestrict or complicate the mathematics, to
produce variants of the theory, or to dig out the theory’s fundamental
assumptions, to try to make the analogy fit again.2 Anomaly deepens into
crisis when these attempts fail; when, for example, the complexity of the
theory increases faster than its accuracy*; or, the area of trouble grows
larger, and not smaller, until the very fundamentals of the paradigm are
thrown in question‘; or, some rank outsiders with a quite different view-
point and rudimentary new technique succeed in solving with ease the
main problem which was causing all the trouble, so that the whole present
paradigm, together with all its commitments, derivations, and assump-
tions, is made to look dreamlike. Putting it more generally, it is not only
the case that a fully extended paradigm, or theory, reaches a point where
further extensions of it produce diminishing returns. The situation is
worse. The paradigm itself goes bad on you, if it is stretched too far, pro-
ducing conceptual inconsistency, absurdity, misexpectation, disorder,
complexity and confusion, in exactly the same way as a crude analogy does,
if pressed too far, say, in a poem, but quite unlike the way in which a
system of pure mathematics does, when it yields undecidable formulae or
contradictions, or fails to yield proofs; i.e. when an exact statement of
what has gone wrong can still be made.

No philosopher of science before Kuhn had described this deterioration.
All had blamed the gradual collapse of various scientific theories on the
fact that they were eventually falsified in experience by, say, the emergence
of new facts; i.e. on the non-cooperation, as it were, of nature. None had

had previously been standard, are rejected as metaphysical, as the concern of another
discipline, or sometimes as just too problematic to be worth the time.’ For examples of
basic problems which later science rendered ‘invisible’, see pp. 103-7; for the general
discussion of the ‘invisibility’, see the whole chapter on Revolutions as Changes in World
View. 1 Hesse [1963], pp. 9 ff.

2 Kuhn [1962], p. go: ‘The proliferation of competing articulations, the willingness to
try anything, the expression of explicit discontent, the recourse to philosophy and to
debate over fundamentals, all these are symptoms of a transition from normal to extra-
ordinary research,’ See also the comparison of crisis-science with pre-paradigm science
(p. 84).

3 Kuhn [1962], pp. 68-70. * Ibid. p. 65.

84 MARGARET MASTERMAN

blamed it on the fact that theories, since they have to have concrete analo-
gical paradigms at the heart of them to define their basic commitments,
and since the effect of these paradigms is drastically to restrict their fields,
collapse, when extended too far, by their own make-up; without any
necessary accentuating irritation from nature at all.

And now, to end, we get to the heart of the matter: that of envisaging a
crude analogy as an artefact. And the heart of considering this consists in
asking the question: ‘How does a crude paradigm extend itself?’, or ‘What
(if anything) does Kuhn mean by “replication”?

I will start with the second question, since it leads to the first. One sign
that Kuhn takes seriously the notion that normal science consists of puzzle-
solving (and therefore that a paradigm has got to be an artefact) is that he
immediately asks himself (p. 38), ‘If there is puzzle-solving, where are the
rules?’ He is then brought up short (pp. 42-6) by the fact that, three quar-
ters of the time, there are no rules. Faced with his own inability to find any
rules, Kuhn then takes two incompatible ways out. The first (pp. 42-4) is to
assert tough-mindedly that there need not be any rules. The second, char-
acteristically, is to say (pp. 38-9) that by ‘rule’ he did not really mean
‘rule’, but ‘preconception’, or ‘established viewpoint’. This second sugges-
tion, in puzzle-solving, just won’t do, for rules either are rules or they are
not; and that Kuhn knows this, really, is shown by the fact that thence-
forward, and indeed throughout the book, he pursues his own first enter-
prise of trying to find out how paradigms operate independently of rules.
His suggestions are the following. Maybe, he says, paradigms add new
developments and parts to themselves by exploiting a ‘network of over-
lapping and crisscross’ Wittgensteinian ‘family resemblances’ (p. 45), each
resemblance only holding with regard to some properties and between some
of the parts. Or perhaps paradigms ‘may relate by resemblance and by
modelling to one or another part of the scientific corpus which the com-
munity in question already recognizes as among its established achieve-
ments...’ (p. 45). Earlier (p. 23), in defining ‘paradigm’, he had talked
about an exact grammatical replication-relation which, however, he said
‘rarely holds between a paradigm and its exemplifications’; and later
(pp. 32 ff.) he talks of the ‘articulation’ or ‘reformulation’ of a paradigm as
a process which, when it occurs in a qualitative science, cannot be de-
scribed in terms of normal mathematical inference. Of course, it may be that
all these Kuhnian resemblance-relations do not form a genus: they may all
essentially differ from one another; but again (see above, the diseussion of
the different senses of ‘paradigm’) if they do, Kuhn, philosophically speak-
ing, is saying nothing definite at all. If, however, they do form a genus; and
still more, if—as I shall from now on presuppose—they are all different

THE NATURE OF A PARADIGM 85

ways of doing the same thing; then Kuhn is indeed saying something
philosophically new.

Within normal science (says Kuhn, on this reading) paradigms are cap-
able of expansion and development in two quite different ways. They
develop, in the end, by mathematical or other rule-governed inference—
which alone enables true puzzles to be solved. But they also develop,
initially, by intuitive ‘articulation’ (or ‘family resemblance’, or, ‘direct
modelling’, or ‘replication’, in an extended sense—any or all of these).
This second process also is a form of inference in a wider sense of ‘in-
ference’—in that sense in which ‘inference’ is literally any kind of per-
mission to pass from one unit or sequence of units or states of affairs to
another unit or sequence of units or states of affairs—but it is intuitive; it
does not go by rules.

And this brings us back to our first question, of how a crude paradigm
extends itself. If the answer is, ‘By intuitive inference’, we then ask: ‘What
is this so-called intuitive inference, and is it really intuitive?’ For if there
is One operation more than another which is not intuitive, it is the entirely
mechanizable operation of marking a replica, B’, of an original, B. This
replication cannot therefore be what Kuhn means. He much more means,
that when B’ is a replication of B, B’ reproduces what, for some known
purpose, P, are taken to be the main features of B. When a mathematical
model, M, for instance, is ‘hung on to’ a crude paradigm, C, in the manner
which we have been describing, M, for some P, reproduces the main
features of C. It may be, as Max Black says,! in describing this model-
original form of relation, that many of what superficially seem to be the
main features of MM—for instance, its scale—may be irrelevant to building
up the replication between M and C; they are not included in the state-
ment of the purpose P. But, as between M and C, there must be some
corresponding main features; otherwise, we should not say that MM is a
model of C.

Now there are two forms of formal thinking which are relevant to the
analysis of main-feature replication; both of these have emerged from the
computer sciences. The first of these, on which there is now quite a
literature,” is the mathematics of classification, or of ‘clumps’; i.e. the
formalization of the process of finding Wittgensteinian families. The
second of these, on which there is almost no literature, apart from the
general literature on mechanized pattern recognition,® is the set of

1 Black [1962], pp. 219-23. As Black shows, the model-original form of relation tends
to be, in reality, more complicated than I have here defined it.

? Parker-Rhodes and Needham [1960]; Parker-Rhodes [1961]; Needham [1961a] and

[1961b]; Needham [1963]; Needham and Sparck-Jones [1964] and Needham [196s).
3 See, for example, Barus [1962}.

86 MARGARET MASTERMAN

procedures for making a digital computer make an ‘inexact match’ between
two formulae which are highly similar to one another, but not quite the same.

In both of these methods, the conglomerates of data in question have to
be characterized by reference to a set of properties with regard to which an
answer can always be given to the question, ‘Has this conglomerate this
property or not?’ If it has, a 7 is written in its characteristics; if not, an 0.
At the end of the characterization, binary numbers of equal lengths will
have been produced for all the conglomerates of data; and, for the case of
all pieces of data which, according to the characterization, come out exactly
the same, the binary numbers, of course, come out equal. But for the cases
in which there is ‘some similarity’, as we say, but not complete likeness,
two things can be done: (a) in the mathematics of clumps, a similarity-
criterion can be formulated, according to which all conglomerates scrut-
inized as similar will come out as being in the same family or clump; or
(b) weight some properties of the data, or some combinations of properties
of the data, as ‘main features’ of the data, in such a way that a unique
answer can be given to the question, ‘Which, of all the set of conglomerates
of data, D,...D,, is “most similar in its main features” to another con-
glomerate of data, D’, which comes from outside the set; i.e. which D
“inexactly matches” with D’?’ It is this last procedure which is so exceed-
ingly difficult to reduce to programme-form (not that the programming of
the mathematics of clumps itself is easy); in fact, it is so difficult that it is a
well-known non-numerical data-programmer’s horror.? Nevertheless, a
strong prima facie case could be made for saying that this ‘inexact matching’,
if and when it can be achieved, is the ‘replication-relation’ which we are
looking for. It is not certain in what sense it is a relation: it is reflexive and
symmetric, for instance, but not transitive (from the fact that A has its
main features similar to those of B, and B to those of C, it by no means
follows that A has its main features similar to those of C, unless each
replication has an identical P). Thus replication-logic, in its crude state,
cited in note is a one-step-at-a-time logic which never gets off the ground; a

1 Various similarity-criteria are mentioned in the papers cited in note 2 to p. 85 above.
The earliest to be formulated was that of Tanimoto [1958]. See also, Sneath and Sokal
[1963].

2 A vicious infinite regress is apt to set in of the following form:

(i) the tests for similarity of main features over a certain threshold cannot be applied
until tests for mainness of feature have first been applied. A second calculus of
mainness has thus to be created.

(ii) the tests for mainness of feature cannot be applied until they have first been ordered
since they turn out not to be independent of each other. A third calculus giving the
ordering of the criteria for testing mainness of feature thus has to be created.

(iii) These ordering-considerations themselves depend on bracketing-considerations
«++ (etc.).

In other words, the process of progressive detection of complexity increases faster than the
invention of means of dealing with it.

THE NATURE OF A PARADIGM 87

logic in which the whole putative effort is to see under what conditions, and
with what weighting, and with what feedback of information to change the
weighting, and at what cost to the richness and completeness of the charac-
terization scheme, a limited amount of recursiveness within some par-
ticular sequential pattern of replications, can be established. One feature
of the logic is always transitive, namely that of temporal succession; for if
A occurs earlier in a replication-sequence than B, and B than C, then A
occurs earlier than C; and this can be important if what is being studied is
the gradual accentuation, through a sequence of sequences of replication,
each feeding back output into some other, of some prechosen main feature.

It is not even certain that replication is, strictly speaking, a form of
inference. I do not see, for instance, how any inference-theorem could be
proved of it. In fact, when contrasted with normal simple deduction,
replication, and controlling replications, is logically horrible. It is how-
ever what of all things, the human brain in its unconscious recognition-
processes seems most easily to do; the artificial intelligence men have now
thrown new light on it}; and it is (I think) how Kuhn’s paradigm extends
itself. Quite a few very simply replicating-systems have actually been made;
within the field of information-retrieval, for instance, any retrieval algorithm
which has a scale-of-relevance-procedure attached to it counts as a replica-
tion-system within the description which I have given, as does any search-
procedure which distinguishes main features and which is built into a
character-reader. But such procedures have not yet been thought of in
general terms, so that no general analysis of the operation of main-feature
recognition has as yet been made.

In view of the obvious difficulties of handling, even with a machine,
such an entity as Kuhn’s crude paradigm has turned out to be (that is, if I
am right as to what it has turned out to be) and in view of the obvious
scepticism which even the suggestion that we should take Kuhn’s paradigm
seriously and philosophically is bound to arouse, it is worth reminding our-
selves, in a final paragraph, of what happens if we do not follow up Kuhn’s
thought any further; i.e. what happens if we drop his whole paradigm
idea?

It may be difficult both to ascertain Kuhn’s thought, and to develop it;
but if we do not make the effort to do this, then it seems to me that we are
left in a very disturbing position indeed. For, as historians, however much
we may cavil at Kuhn’s conclusions in detail, we are not going to be able to
go back to where we were before Kuhn and his immediate predecessors
began to get at us. Their protest against the unconscious dishonesty and
the swings of bias with which the history of science has been done in

2 See particularly, the notion of ‘regeneration’ in Good [1965].

88 MARGARET MASTERMAN

scientific textbooks up to now cuts far too deep; and so does their outcry
against the oversimple and distorted accumulative view of science which
has resulted from reading the textbooks as though they were the real
history. On the other hand, if no more adequate overall view of science
results, in the end, from doing the history of science better, what is the
point of doing this history at all—except perhaps as an esoteric hobby?
The history of science, by its nature as part of the history of ideas, has got
to be a discipline which helps actual scientists to get a deeper insight into
the real nature of their own science. If it does not do this, it becomes
trivial—the activity of making a pedagogic collection of, in themselves,
minor facts. So, if we retreat from all further consideration of Kuhn’s ‘new
image’ of science, we run the risk of totally disconnecting the new-style
realistic history of science from its old-style philosophy: a disaster.

And if we go forward, and if I am right in my analysis, we have got to
re-examine what is true of analogy in the light of what Kuhn has shown to
be true of paradigms.

REFERENCES

Barus [1962]; ‘A Scheme for Recognizing Patterns for an Unspecified Class’, in Fischer,
Pollock, Raddack and Stevens (eds.): Optical Character Recognition, 1962.

Black [1962]: Models and Metaphors, 1962.

Brodbeck [1962]: ‘Explanation, Prediction and “Imperfect Knowledge” ’, in Feigl and
Maxwell (eds.): Minnesota Studies in the Philosophy of Science, 3, pp. 231-72+

Campbell [1920]: Foundations of Science, 1920.

Feyerabend [1962]: ‘Explanation, Reduction and Empiricism’, in Feigl and Maxwell
(eds.): Minnesota Studies in the Philosophy of Science, 3, pp. 28-97.

Good [1965]: Speculations Concerning the First Ultra-Intelligent Machine, 1965.

Gregory [1966]: Eye and Brain, 1966.

Hesse [1963]: Models and Analogies in Science, 1963.

Hesse [1964]: “The Explanatory Function of Metaphor’, in Bar-Hillel (ed.): Logic, Metho-
dology and Philosophy of Science, 1966, pp. 249~59.

Jevons [1873]: The Principles of Science, 1873.

Kuhn [1962]: The Structure of Scientific Revolutions, 1962.

Lakatos [1963-64]: ‘Proofs and Refutations’, The British Journal for the Philosophy of
Science, 14, pp. 1-25, 120-39, 221~43 and 296-342.

Needham [1961a]: ‘The Theory of Clumps, II’, Cambridge Language Research Unit
Working Papers, 139.

Needham [1961b]: ‘Research on Information Retrieval, Classification and Clumping,
1957-61’, Ph.D. Thesis, Cambridge 1961.

Needham [1963]: ‘A Method for Using Computers in Information Classification’, in
Information Process 62: Proceedings of the International Federation for Information
Processing Congress, Amsterdam, 1962.

Needham and Sparck Jones [1964]: ‘Keywords and Clumps’, Journal ef Documentation,
20, no. 1.

Needham [1965]: ‘Applications of the Theory of Clumps’, Mechanical Translation, 8,
PP. 113-27.

Parker-Rhodes and Needham [1960]: ‘The Theory of Clumps’, Cambridge Language
Research Unit Working Papers, 126.

THE NATURE OF A PARADIGM 89

Parker-Rhodes [1961]: ‘Contributions to the Theory of Clumps’, Cambridge Language
Research Unit Working Papers, 138.

Popper [1963]: Conjectures and Refutations, 1963.

Putnam [1962]: “The Analytic and the Synthetic’, in Feigl and Maxwell (eds.): Minnesota
Studies in the Philosophy of Science, 3, pp. 358-07.

Sneath and Sokal [1963]: Principles of Numerical Taxonomy, 1963.

Tanimoto [1958]: ‘An Elementary Mathematical Theory of Classification and Prediction’
I.B.M. Research, 1958.

Falsification and the Methodology of
Scientific Research Programmes’

IMRE LAKATOS
London School of Economics

1. Science: reason or religion?
2. Fallibilism versus falsificationism.
(a) Dogmatic (or naturalistic) falsificationism. The empirical basis.
(b) Methodological falsificationism. The ‘empirical basis’.
(c) Sophisticated versus naive falsificationism. Progressive and degener-
ating problemshifts.
3. A methodology of scientific research programmes.
(a) Negative heuristic; the ‘hard core’ of the programme.
(5) Positive heuristic; the construction of the ‘protective belt’ and the
relative autonomy of theoretical science.
(c) Two illustrations: Prout and Bohr.
(cz) Prout: a research programme progressing in an ocean of anomalies.
(cz) Bohr: a research programme progressing on inconsistent founda-
tions.
(d) A new look at crucial experiments: the end of instant rationahty.
(dt) The Michelson—Morley experiment.
(d2) The Lummer—Pringsheim experiments.
(d3) Beta-decay versus conservation laws.
(d4) Conclusion. The requirement of continuous growth.
4. The Popperian versus the Kuhnian research programme.
Appendix: Popper, falsificationism and the ‘Duhem-Quine thesis’.

I. SCIENCE! REASON OR RELIGION?

For centuries knowledge meant proven knowledge—proven either by the
power of the intellect or by the evidence of the senses. Wisdom and intellec-
tual integrity demanded that one must desist from unproven utterances
and minimize, even in thought, the gap between speculation and estab-
lished knowledge. The proving power of the intellect or the senses was

? This paper is a considerably improved version of my [19688] and a crude version of
my [1970]. Some parts of the former are here reproduced without change with the per-
mission of the Editor of the Proceedings of the Aristotelian Society. In the preparation
of the new version I received much help from Tad Beckman, Colin Howson, Clive
Kilmister, Larry Laudan, Eliot Leader, Alan Musgrave, Michael Sukale, John Watkins
and John Worrall.

g2 IMRE LAKATOS

questioned by the sceptics more than two thousand years ago; but they
were browbeaten into confusion by the glory of Newtonian physics.
Einstein’s results again turned the tables and now very few philosophers
or scientists still think that scientific knowledge is, or can be, proven
knowledge. But few realize that with this the whole classical structure of
intellectual values falls in ruins and has to be replaced: one cannot simply
water down the ideal of proven truth—as some logical empiricists do—to
the ideal of ‘probable truth’! or—as some sociologists of knowledge do—to
‘truth by [changing] consensus’.?

Popper’s distinction lies primarily in his having grasped the full impli-
cations of the collapse of the best-corroborated scientific theory of all
times: Newtonian mechanics and the Newtonian theory of gravitation. In
his view virtue lies not in caution in avoiding errors, but in ruthlessness in
eliminating them. Boldness in conjectures on the one hand and austerity
in refutations on the other: this is Popper’s recipe. Intellectual honesty
does not consist in trying to entrench, or establish one’s position by
proving (or ‘probabilifying’) it—intellectual honesty consists rather in
specifying precisely the conditions under which one is willing to give up
one’s position. Committed Marxists and Freudians refuse to specify such
conditions: this is the hallmark of their intellectual dishonesty. Belief may
be a regrettably unavoidable biological weakness to be kept under the con-
trol of criticism: but commitment is for Popper an outright crime.

Kuhn thinks otherwise. He too rejects the idea that science grows by
accumulation of eternal truths.? He too takes his main inspiration from
Einstein’s overthrow of Newtonian physics. His main problem too is
scientific revolution. But while according to Popper science is ‘revolution
in permanence’, and criticism the heart of the scientific enterprise, accord-
ing to Kuhn revolution is exceptional and, indeed, extra-scientific, and
criticism is, in ‘normal’ times, anathema. Indeed for Kuhn the transition

1 The main contemporary protagonist of the ideal of ‘probable truth’ is Rudolf Carnap.
For the historical background and a criticism of this position, cf. Lakatos [1968].

2 The main contemporary protagonists of the ideal of ‘truth by consensus’ are Polanyi
and Kuhn. For the historical background and a criticism of this position, cf. Musgrave
[1969a], Musgrave [1969b] and Lakatos [1970].

3 Indeed he introduces his [1962] by arguing against the ‘development-by-accumulation’
idea of scientific growth. But his intellectual debt is to Koyré rather than to Popper.
Koyré showed that positivism gives bad guidance to the historian of science, for the
history of physics can only be understood in the context of a succession of ‘metaphysical’
research programmes. Thus scientific changes are connected with vast cataclysmic
metaphysical revolutions. Kuhn develops this message of Burtt and Koyré and the vast
success of his book was partly due to his hard-hitting, direct criticism of justificationist
historiography—which created a sensation among ordinary scientists and historians of

science whom Burtt’s, Koyré’s (or Popper’s) message has not yet reached. But, un-
fortunately, his message had some authoritarian and irrationalist overtones.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 93

from criticism to commitment marks the point where progress—and
‘normal’ science—begins. For him the idea that on ‘refutation’ one can
demand the rejection, the elimination of a theory, is ‘naive’ falsificationism.
Criticism of the dominant theory and proposals of new theories are only
allowed in the rare moments of ‘crisis’. This last Kuhnian thesis has been
widely criticized! and I shall not discuss it. My concern is rather that
Kuhn, having recognized the failure both of justificationism and falsi-
ficationism in providing rational accounts of scientific growth, seems now
to fall back on irrationalism.

For Popper scientific change is rational or at least rationally reconstruct-
ible and falls in the realm of the logic of discovery. For Kuhn scientific
change—from one ‘paradigm’ to another—is a mystical conversion which
is not and cannot be governed by rules of reason and which falls totally
within the realm of the (social) psychology of discovery. Scientific change is
a kind of religious change.

The clash between Popper and Kuhn is not about a mere technical
point in epistemology. It concerns our central intellectual values, and has
implications not only for theoretical physics but also for the underdeveloped
social sciences and even for moral and political philosophy. If even in
science there is no other way of judging a theory but by assessing the
number, faith and vocal energy of its supporters, then this must be even
more so in the social sciences: truth lies in power. Thus Kuhn’s position
would vindicate, no doubt, unintentionally, the basic political credo of
contemporary religious maniacs (‘student revolutionaries’).

In this paper I shall first show that in Popper’s logic of scientific dis-
covery two different positions are conflated. Kuhn understands only one
of these, ‘naive falsificationism’ (I prefer the term ‘naive methodological
falsificationism’); I think that his criticism of it is correct, and I shall even
strengthen it. But Kuhn does not understand a more sophisticated position
the rationality of which is not based on ‘naive’ falsificationism. I shall try
to explain—and further strengthen—this stronger Popperian position
which, I think, may escape Kuhn’s strictures and present scientific revolu-
tions as constituting rational progress rather than as religious conversions.

2. FALLIBILISM VERSUS FALSIFICATIONISM

(a) Dogmatic (or naturalistic) falsificationism. The empirical basis.

To see the conflicting theses more clearly, we have to reconstruct the prob-
lem situation as it was in philosophy of science after the breakdown of ‘justi-
ficationism’.

1 Cf. e.g. Watkins’s and Feyerabend’s contributions to this volume.

94 IMRE LAKATOS

According to the ‘justificationists’ scientific knowledge consisted of proven
propositions. Having recognized that strictly logical deductions enable us
only to infer (transmit truth) but not to prove (establish truth), they dis-
agreed about the nature of those propositions (axioms) whose truth can be
proved by extra-logical means. Classical intellectualists (or ‘rationalists’ in
the narrow sense of the term) admitted very varied—and powerful—sorts
of extralogical ‘proofs’ by revelation, intellectual intuition, experience.
These, with the help of logic, enabled them to prove every sort of scien-
tific proposition. Classical empiricists accepted as axioms only a relatively
small set of ‘factual propositions’ which expressed the ‘hard facts’. ‘Their
truth-value was established by experience and they constituted the empiri-
cal basis of science. In order to prove scientific theories from nothing else
but the narrow empirical basis, they needed a logic much more powerful
than the deductive logic of the classical intellectualists: ‘inductive logic’. All
justificationists, whether intellectualists or empiricists, agreed that a
singular statement expressing a ‘hard fact’ may disprove a universal theory};
but few of them thought that a finite conjunction of factual propositions
might be sufficient to prove ‘inductively’ a universal theory.”

Justificationism, that is, the identification of knowledge with proven
knowledge, was the dominant tradition in rational thought throughout the
ages. Scepticism did not deny justificationism: it only claimed that there

was (and could be) no proven knowledge and therefore no knowledge :

whatsoever. For the sceptics ‘knowledge’ was nothing but animal belief.
Thus justificationist scepticism ridiculed objective thought and opened the
door to irrationalism, mysticism, superstition.

This situation explains the enormous effort invested by classical rational-
ists in trying to save the synthetical a priori principles of intellectualism
and by classical empiricists in trying to save the certainty of an empirical
basis and the validity of inductive inference. For all of them scientific
honesty demanded that one assert nothing that is unproven. However, both
were defeated: Kantians by non-Euclidean geometry and by non-New-
tonian physics, and empiricists by the logical impossibility of establishing

1 Justificationists repeatedly stressed this asymmetry between singular factual state-
ments and universal theories. Cf. e.g. Popkin’s discussion of Pascal in Popkin [1968], p. 14
and Kant’s statement to the same effect as quoted in the new motio of the third 1969
German edition of Popper’s Logik der Forschung. (Popper’s choice of this time-honoured
cornerstone of elementary logic as a motto of the new edition of his classic shows his
main concern: to fight probabilism, in which this asymmetry becomes irrelevant; for
probabilists theories may become almost as well established as factual propositions.)

2 Indeed, even some of these few shifted, following Mill, the rather obviously insoluble
problem of inductive proof (of universal from particular propositions) to the slightly
less obviously insoluble problem of proving particular factual propositions from other
particular factual propositions.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 95

an empirical basis (as Kantians pointed out, facts cannot prove proposi-
tions) and of establishing an inductive logic (no logic can infallibly in-
crease content). It turned out that all theories are equally unprovable.

Philosophers were slow to recognize this, for obvious reasons: classical
justificationists feared that once they conceded that theoretical science is
unprovable, they would have also to concede that it is sophistry and illu-
sion, a dishonest fraud. The philosophical importance of probabilism (or
‘neojustificationism’) lies in the denial that such a concession is necessary.

Probabilism was elaborated by a group of Cambridge philosophers who
thought that although scientific theories are equally unprovable, they have
different degrees of probability (in the sense of the calculus of probability)
relative to the available empirical evidence.' Scientific honesty then requires
less than had been thought: it consists in uttering only highly probable theories;
or even in merely specifying, for each scientific theory, the evidence, and the
probability of the theory tn the light of this evidence.

Of course, replacing proof by probability was a major retreat for justi-
ficationist thought. But even this retreat turned out to be insufficient.
It was soon shown, mainly by Popper’s persistent efforts, that under very
general conditions all theories have zero probability, whatever the evi-
dence; all theories are not only equally unprovable but also equally improb-
able.”

Many philosophers still argue that the failure to obtain at least a prob-
abilistic solution of the problem of induction means that we ‘throw over
almost everything that is regarded as knowledge by science and common
sense.’ It is against this background that one must appreciate the dram-
atic change brought about by falsificationism in evaluating theories, and in
general, in the standards of intellectual honesty. Falsificationism was, in a
sense, a new and considerable retreat for rational thought. But since it was
a retreat from utopian standards, it cleared away much hypocrisy and
muddled thought, and thus, in fact, it represented an advance.

First I shall discuss a most important brand of falsificationism: dogmatic
(or ‘naturalistic’)* falsificationism. Dogmatic falsificationism admits the
fallibility of all scientific theories without qualification, but it retains a sort
of infallible empirical basis. It is strictly empiricist without being induc-
tivist: it denies that the certainty of the empirical basis can be transmitted

1 The founding fathers of probabilism were intellectualists; Carnap’s later efforts to
build up an empiricist brand of probabilism failed. Cf. my [1968a], p. 367 and also p. 361,
footnote 2.

* For a detailed discussion, cf. my [1968a], especially pp. 353 ff.

5 Russell [1943], p. 683. For a discussion of Russell’s justificationism, cf. my [1962],
especially pp. 167 ff.

‘ For the explanation of this term, cf. below, p. 98, footnote 1.

96 IMRE LAKATOS

to theories. Thus dogmatic falsificationism is the weakest brand of justifica-
tionism.

It is extremely important to stress that admitting [fortified] empirical
counterevidence as a final arbiter against a theory does not make one a dog-
matic falsificationist. Any Kantian or inductivist will agree to such arbi-
tration. But both the Kantian and the inductivist, while bowing to a nega-
tive crucial experiment, will also specify conditions of how to establish,
entrench one unrefuted theory more than another. Kantians held that
Euclidean geometry and Newtonian mechanics were established with
certainty; inductivists held they had probability 1. For the dogmatic
falsificationist, however, empirical counterevidence is the one and only
arbiter which may judge a theory.

The hallmark of dogmatic falsificationism is then the recognition that all
theories are equally conjectural. Science cannot prove any theory. But
although science cannot prove, it can disprove: it ‘can perform with com-
plete logical certainty [the act of] repudiation of what is false’, that is,
there is an absolutely firm empirical basis of facts which can be used to
disprove theories. Falsificationists provide new—very modest—standards
of scientific honesty: they are willing to regard a proposition as ‘scientific’
not only if it is a proven factual proposition, but even if it is nothing more
than a falsifiable one, that is, if there are factual propositions available at
the time with which it may clash, or, in other words, if it has potential
falsifiers.?

Scientific honesty then consists of specifying, in advance, an experiment
such that tf the result contradicts the theory, the theory has to be given up. The
falsificationist demands that once a proposition is disproved, there must be
no prevarication: the proposition must be unconditionally rejected. To
(non-tautologous) unfalsifiable propositions the dogmatic falsificationist
gives short shrift: he brands them ‘metaphysical’ and denies them scien-
tific standing.

Dogmatic falsificationists draw a sharp demarcation between the
theoretician and the experimenter: the theoretician proposes, the experi-
menter—in the name of Nature—disposes. As Weyl put it: ‘I wish to
record my unbounded admiration for the work of the experimenter in his
struggle to wrest interpretable facts from an unyielding Nature who knows
so well how to meet our theories with a decisive No—or with an inaudible

1 Medawar [1967], p. 144.

2'This discussion already indicates the vital importance of a demarcation between
provable factual and unprovable theoretical propositions for the dogmatic falsificationist.

3 ‘Criteria of refutation have to be laid down beforehand: it must be agreed which

observable situations, if actually observed, mean that the theory is refuted’ (Popper
[1963], p. 38, footnote 3).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 97

Yes.’! Braithwaite gives a particularly lucid exposition of dogmatic falsi-
ficationism. He raises the problem of the objectivity of science: “To what
extent, then, should an established scientific deductive system be regarded
as a free creation of the human mind, and to what extent should it be
regarded as giving an objective account of the facts of nature?’. His answer is:
‘The form of a statement of ascientific hypothesis and its use toexpress a gen-
eral proposition, is a human device; what is due to Nature are the observable
facts which refute or fail to refute the scientifichypothesis . . . [Inscience] we
hand over to Nature the task of deciding whether any of the contingent low-
est-level conclusions are false. This objective test of falsity it is which
makes the deductive system, in whose construction we have very great free-
dom, a deductive system of scientific hypotheses. Man proposes a system of
hypotheses: Nature disposes of its truth or falsity. Man invents a scientific
system, and then discovers whether or not it accords with observed
fact.’*

According to the logic of dogmatic falsificationism, science grows by repeated
overthrow of theories with the help of hard facts. For instance, according to
this view, Descartes’s vortex theory of gravity was refuted—and elimi-
nated—by the fact that planets moved in ellipses rather than in Cartesian
circles; Newton’s theory, however, explained successfully the then avail-
able facts, both those which had been explained by Descartes’s theory and
those which refuted it. Therefore Newton’s theory replaced Descartes’s
theory. Analogously, as seen by falsificationists, Newton’s theory was, in
turn, refuted—proved false—by the anomalous perihelion of Mercury,
while Einstein’s explained that too. Thus science proceeds by bold specu-
lations, which are never proved or even made probable, but some of which
are later eliminated by hard, conclusive refutations and then replaced by
still bolder, new and, at least at the start, unrefuted speculations.

Dogmatic falsificationism, however, is untenable. It rests on two false
assumptions and on a too narrow criterion of demarcation between scien-
tific and non-scientific.

The first assumption is that there is a natural, psychological borderline
between theoretical or speculative propositions on the one hand and
factual or observational (or basic) propositions on the other. (I shall call
this—following Popper—the naturalistic doctrine of observation.)

The second assumption is that if a proposition satisfies the psychological

1 Quoted in Popper [1934], section 85, with Popper’s comment: ‘I fully agree.’

? Braithwaite [1953], pp. 367-8. For the ‘incorrigibility’ of Braithwaite’s observed
facts, cf. his [1938]. While in the quoted passage Braithwaite gives a forceful answer to
the problem of scientific objectivity, in another passage he points out that ‘except for the

straightforward generalizations of observable facts... complete refutation is no more
possible than is complete proof’ ([1953], p. 19). Also cf. below, p. 113, footnote 4.

98 IMRE LAKATOS

criterion of being factual or observational (or basic) then it is true; one
may say that it was proved from facts. (I shall call this the doctrine of
observational (or experimental) proof.)'

These two assumptions secure for the dogmatic falsificationist’s deadly
disproofs an empirical basis from which proven falsehood can be carried
by deductive logic to the theory under test.

These assumptions are complemented by a demarcation criterion: only
those theories are ‘scientific’ which forbid certain observable states of
affairs and therefore are factually disprovable. Or, a theory ts ‘scientific’ if it
has an empirical basis.?

But both assumptions are false. Psychology testifies against the first,
logic against the second, and, finally, methodological judgment testifies
against the demarcation criterion. I shall discuss them in turn.

(1) A first glance at a few characteristic examples already undermines the
first assumption. Galileo claimed that he could ‘observe’ mountains on the
moon and spots on the sun and that these ‘observations’ refuted the time-
honoured theory that celestial bodies are faultless crystal balls. But his
‘observations’ were not ‘observational’ in the sense of being observed by
the—unaided—senses: their reliability depended on the reliability of his
telescope—and of the optical theory of the telescope—which was violently
questioned by his contemporaries. It was not Galileo’s—pure, untheo-
retical—observations that confronted Aristotelian theory but rather Galileo’s
‘observations’ in the light of his optical theory that confronted the Aris-
totelians’ ‘observations’ in the light of their theory of the heavens. This
leaves us with two inconsistent theories, prima facia on a par. Some empir-
icists may concede this point and agree that Galileo’s ‘observations’ were
not genuine observations; but they still hold that there is a ‘natural de-
marcation’ between statements impressed on an empty and passive mind
directly by the senses—only these constitute genuine ‘immediate know-
ledge’—and between statements which are suggested by impure, theory-
impregnated sensations. Indeed, all brands of justificationist theories of

knowledge which acknowledge the senses as a source (whether as one

1 For these assumptions and their criticism, cf. Popper [1934], sections 4 and 1o. It
is because of this assumption that—following Popper—lI call this brand of falsificationism
‘naturalistic’. Popper’s ‘basic propositions’ should not be confused with the basic propo-
sitions discussed in this section; cf. below, p. 106, footnote 4.

It is important to point out that these two assumptions are also shared by many justi-
ficationists who are not falsificationists: they may add to experimental proofs ‘intuitive
proofs’—as did Kant—or ‘inductive proofs’—as did Mill. Our falsificationist accepts
experimental proofs only.

2 The empirical basis of a theory is the set of its potential falsifiers: the set of those
observational propositions which may disprove it.

3 Incidentally, Galileo also showed—with the help of his optics—that if the moon was
a faultless crystal ball, it would be invisible (Galileo [1632]).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 99

source or as the source) of knowledge are bound to contain a psychology of
observation. Such psychologies specify the ‘right’, ‘normal’, ‘healthy’,
‘unbiased’, ‘careful’ or ‘scientific’ state of the senses—or rather the state of
mind as a whole—in which they observe truth as it is. For instance,
Aristotle—and the Stoics—thought that the right mind was the medically
healthy mind. Modern thinkers recognized that there is more to the right
mind than simple ‘health’. Descartes’s right mind is one steeled in the fire
of sceptical doubt which leaves nothing but the final loneliness of the
cogito in which the ego can then be re-established and God’s guiding hand
found to recognize truth. All schools of modern justificationism can be
characterized by the particular psychotherapy by which they propose to
prepare the mind to receive the grace of proven truth in the course of a
mystical communion. In particular, for classical empiricists the right mind
is a tabula rasa, emptied of all original content, freed from all prejudice of
theory. But it transpires from the work of Kant and Popper—and from the
work of psychologists influenced by them—that such empiricist psycho-
therapy can never succeed. For there are and can be no sensations unim-
pregnated by expectations and therefore there is no natural (i.e. psycholo-
gical) demarcation between observational and theoretical propositions.

(2) But even if there was such a natural demarcation, logic would still
destroy the second assumption of dogmatic falsificationism. For the truth-
value of the ‘observational’ propositions cannot be indubitably decided: no
factual proposition can ever be proved from an experiment. Propositions can
only be derived from other propositions, they cannot be derived from facts:
one cannot prove statements from experiences—‘no more than by thump-
ing the table.’ This is one of the basic points of elementary logic, but one
which is understood by relatively few people even today.*

If factual propositions are unprovable then they are fallible. If they are
fallible then clashes between theories and factual propositions are not
‘falsifications’ but merely inconsistencies. Our imagination may play a
greater role in the formulation of ‘theories’ than in the formulation of

1 True, most psychologists who turned against the idea of justificationist sensationalism
did so under the influence of pragmatist philosophers like William James who denied the
possibility of any sort of objective knowledge. But, even so, Kant’s influence through
Oswald Kiilpe, Franz Brentano and Popper’s influence through Egon Brunswick and
Donald Campbell played a role in the shaping of modern psychology; and if psychology
ever vanquishes psychologism, it will be due to an increased understanding of the Kant-
Popper mainline of objectivist philosophy.

2 Cf. Popper [1934], section 29.

3 Tt seems that the first philosopher to emphasize this might have been Fries in 1837
(cf. Popper [1934], section 29, footnote 3). This is of course a special case of the general
thesis that logical relations, like probability or consistency, refer to propositions. Thus,
for instance, the proposition ‘nature is consistent’ is false (or, if you wish, meaningless),
for nature is not a proposition (or a conjunction of propositions).

100 IMRE LAKATOS

‘factual propositions’,! but they are both fallible. Thus we cannot prove
theories and we cannot disprove them either.* The demarcation between the
soft, unproven ‘theories’ and the hard, proven ‘empirical basis’ is non-
existent: all propositions of science are theoretical and, incurably, fallible.

(3) Finally, even if there were a natural demarcation between observation
statements and theories, and even if the truth-value of observation state-
ments could be indubitably established, dogmatic falsificationism would
still be useless for eliminating the most important class of what are
commonly regarded as scientific theories. For even if experiments could
prove experimental reports, their disproving power would still be miser-
ably restricted: exactly the most admired scientific theories simply fail to forbid
any observable state of affairs.

To support this last contention, I shall first tell a characteristic story and
then propose a general argument.

The story is about an imaginary case of planetary misbehaviour. A
physicist of the pre-Einsteinian era takes Newton’s mechanics and his law
of gravitation (NV), the accepted initial conditions, J, and calculates, with
their help, the path of a newly discovered small planet, p. But the planet
deviates from the calculated path. Does our Newtonian physicist consider
that the deviation was forbidden by Newton’s theory and therefore that,
once established, it refutes the theory N? No. He suggests that there must
be a hitherto unknown planet p’ which perturbs the path of p. He calcu-
lates the mass, orbit, etc., of this hypothetical planet and then asks
an experimental astronomer to test his hypothesis. The planet p’ is so small
that even the biggest available telescopes cannot possibly observe it:
the experimental astronomer applies for a research grant to build yet a
bigger one.* In three years’ time the new telescope is ready. Were
the unknown planet p’ to be discovered, it would be hailed as a new

1 Incidentally, even this is questionable. Cf. below, pp. 127 ff.

2 As Popper put it: ‘No conclusive disproof of a theory can ever be produced’; those
who wait for an infallible disproof before eliminating a theory will have to wait for ever
and ‘will never benefit from experience’ ([1934], section 9).

3 Kant and his English follower, Whewell, both realized that all scientific propositions,
whether a priori or a posteriori, are equally theoretical; but both held that they are equally
provable. Kantians saw clearly that the propositions of science are theoretical in the
sense that they are not written by sensations on the tabula rasa of an empty mind, nor
deduced or induced from such propositions. A factual proposition is only a special kind
of theoretical proposition. In this Popper sided with Kant against the empiricist version
of dogmatism. But Popper went a step further: in his view the propositions of science
are not only theoretical but they are all also fallible, conjectural for ever.

4 If the tiny conjectural planet were out of the reach even of the biggest possible optical
telescopes, he might try some quite novel instrument (like a radiotelescope) in order to
enable him to ‘observe it’, that is, to ask Nature about it, even if only indirectly. (The
new ‘observational’ theory may itself not be properly articulated, let alone severely
tested, but he would care no more than Galileo did.)

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES IOI

victory of Newtonian science. But it is not. Does our scientist abandon
Newton’s theory and his idea of the perturbing planet? No. He suggests
that a cloud of cosmic dust hides the planet from us. He calculates the
location and properties of this cloud and asks for a research grant tosend upa
satellite to test his calculations. Were the satellite’s instruments (possibly
new ones, based on a little-tested theory) to record the existence of the
conjectural cloud, the result would be hailed as an outstanding victory for
Newtonian science. But the cloud is not found. Does our scientist abandon
Newton’s theory, together with the idea of the perturbing planet and the
idea of the cloud which hides it? No. He suggests that there is some mag-
netic field in that region of the universe which disturbed the instruments of
the satellite. A new satellite is sent up. Were the magnetic field to be found,
Newtonians would celebrate a sensational victory. But it is not. Is this
regarded as a refutation of Newtonian science? No. Either yet another
ingenious auxiliary hypothesis is proposed or ...the whole story is
buried in the dusty volumes of periodicals and the story never mentioned
again,!

This story strongly suggests that even a most respected scientific theory,
like Newton’s dynamics and theory of gravitation, may fail to forbid any
observable state of affairs.2 Indeed, some scientific theories forbid an event
occurring in some specified finite spatio-temporal region (or briefly, a ‘singular
event’) only on the condition that no other factor (possibly hidden in some
distant and unspecified spatio-temporal corner of the universe) has any
influence on it. But then such theories never alone contradict a ‘basic’ statement:
they contradict at most a conjunction of a basic statement describing a
spatio-temporally singular event and of a universal non-existence state-
ment saying that no other relevant cause is at work anywhere in the
universe. And the dogmatic falsificationist cannot possibly claim that such
universal non-existence statements belong to the empirical basis: that they
can be observed and proved by experience.

Another way of putting this is to say that some scientific theories are
normally interpreted as containing a ceteris paribus clause®: in such cases it
is always a specific theory together with this clause which may be refuted.
But such a refutation is inconsequential for the specific theory under test

1 At least not until a new research programme supersedes Newton’s programme which
happens to explain this previously recalcitrant phenomenon. In this case, the phenomenon
will be unearthed and enthroned as a ‘crucial experiment’; cf. below, pp. 154 ff.

2 Popper asks: ‘What kind of clinical responses would refute to the satisfaction of the
analyst not merely a particular diagnosis but psychoanalysis itself?’ ([1963], p. 38, footnote
3.) But what kind of observation would refute to the satisfaction of the Newtonian not
merely a particular version but Newtonian theory itself?

8 [Added in press:] This ‘ceteris paribus’ clause must not normally be interpreted as a
separate premise. For a discussion, cf. below, p. 186.

102 IMRE LAKATOS

because by replacing the ceteris paribus clause by a different one the specific
theory can always be retained whatever the tests say.

If so, the ‘inexorable’ disproof procedure of dogmatic falsificationism
breaks down in these cases even if there were a firmly established empirical
basis to serve as a launching pad for the arrow of the modus tollens: the
prime target remains hopelessly elusive.? And as it happens, it is exactly the
most important, ‘mature’ theories in the history of science which are prima
facie undisprovable in this way.” Moreover, by the standards of dogmatic
falsificationism all probabilistic theories also come under this head: for no
finite sample can ever disprove a universal probabilistic theory*®; probabil-
istic theories, like theories with a ceteris paribus clause, have no empirical
basis. But then the dogmatic falsificationist relegates the most important
scientific theories on his own admission to metaphysics where rational dis-
cussion—consisting, by his standards, of proofs and disproofs—has no
place, since a metaphysical theory is neither provable nor disprovable. The
demarcation criterion of dogmatic falsificationism is thus still strongly
antitheoretical.

(Moreover, one can easily argue that ceteris paribus clauses are not excep-
tions, but the rule in science. Science, after all, must be demarcated from a
curiosity shop where funny local—or cosmic—oddities are collected and
displayed. The assertion that ‘all Britons died from lung cancer between
1950 and 1960’ is logically possible, and might even have been true. But if
it has been only an occurrence of an event with minute probability, it
would have only curiosity value for the crankish fact-collector, it would
have a macabre entertainment value, but no scientific value. A proposi-
tion might be said to be scientific only if it aims at expressing a causal
connection: such connection between being a Briton and dying of lung
cancer may not even be intended. Similarly, ‘all swans are white’, if true,
would be a mere curiosity unless it asserted that swanness causes whiteness.
But then a black swan would not refute this proposition, since it may only
indicate other causes operating simultaneously. ‘Thus ‘all swans are white’
is either an oddity and easily disprovable or a scientific proposition with a
ceteris paribus clause and therefore undisprovable. Tenacity of a theory
against empirical evidence would then be an argument for rather than against
regarding it as ‘scientific’. ‘Irrefutability’ would become a hallmark of science.‘)

1 Incidentally, we might persuade the dogmatic falsificationist that his demarcation
criterion was a very naive mistake. If he gives it up but retains his two basic assumptions,
he will have to ban theories from science and regard the growth of science as an accumula-
tion of proven basic statements. This indeed is the final stage of classical empiricism after
the evaporation of the hope that facts can prove or at least disprove theories,

2 This is no coincidence; cf. below, pp. 175 ff.

* Cf. Popper [1934], chapter VIII. * For a much stronger case, cf. below, sect. 3.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 103

To sum up: classical justificationists only admitted proven theories;
neoclassical justificationists probable ones; dogmatic falsificationists
realized that in either case no theories are admissible. They decided to
admit theories if they are disprovable—disprovable by a finite number of
observations. But even if there were such disprovable theories—those
which can be contradicted by a finite number of observable facts—they are
still logically too near to the empirical basis. For instance, on the terms of
the dogmatic falsificationist, a theory like ‘All planets move in ellipses’
may be disproved by five observations; therefore the dogmatic falsifica-
tionist will regard it as scientific. A theory like ‘All planets move in circles’
may be disproved by four observations; therefore the dogmatic falsifica-
tionist will regard it as still more scientific. The acme of scientificness will
be a theory like ‘All swans are white’ which is disprovable by one single
observation. On the other hand, he will reject all probabilistic theories
together with Newton’s, Maxwell’s, Einstein’s theories, as unscientific,
for no finite number of observations can ever disprove them.

If we accept the demarcation criterion of dogmatic falsificationism, and
also the idea that facts can prove ‘factual’ propositions, we have to declare
that the most important, if not all, theories ever proposed in the history
of science are metaphysical, that most, if not all, of the accepted progress
is pseudo-progress, that most, if not all, of the work done is irrational. If,
however, still accepting the demarcation criterion of dogmatic falsifica-
tionism, we deny that facts can prove propositions, then we certainly end
up in complete scepticism: then all science is undoubtedly irrational
metaphysics and should be rejected. Scientific theories are not only equally
unprovable, and equally improbable, but they are also equally undisprovable.
But the recognition that not only the theoretical but all the propositions
in science are fallible, means the total collapse of all forms of dogmatic
justificationism as theories of scientific rationality.

(b) Methodological falsificationism. The ‘empirical basis’.

The collapse of dogmatic falsificationism because of fallibilisticarguments
seems to bring us back to square one. If all scientific statements are fallible
theories, one can criticize them only for inconsistency. But then, in what
sense, if any, is science empirical? If scientific theories are neither provable,
nor probabilifiable, nor disprovable, then the sceptics seem to be finally right:
science is no more than vain speculation and there is no such thing as pro-
gress in scientific knowledge. Can we still oppose scepticism? Can we
save scientific criticism from fallibilism? Is it possible to have a fallibil-
istic theory of scientific progress? In particular, if scientific criticism is
fallible, on what ground can we ever eliminate a theory?

104 IMRE LAKATOS

A most intriguing answer is provided by methodological falsificationism.
Methodological falsificationism is a brand of conventionalism; therefore
in order to understand it, we must first discuss conventionalism in
general.

There is an important demarcation between ‘passivist’ and ‘activist’
theories of knowledge. ‘Passivists’ hold that true knowledge is Nature’s
imprint on a perfectly inert mind: mental activity can only result in bias
and distortion. The most influential passivist school is classical empiricism.
‘Activists’ hold that we cannot read the book of Nature without mental
activity, without interpreting them in the light of our expectations or
theories.1 Now conservative ‘activists’ hold that we are born with our basic
expectations; with them we turn the world into ‘our world’ but must then
live for ever in the prison of our world. The idea that we live and die in the
prison of our ‘conceptual frameworks’ was developed primarily by Kant;
pessimistic Kantians thought that the real world is for ever unknowable
because of this prison, while optimistic Kantians thought that God created
our conceptual framework to fit the world.* But revolutionary activists
believe that conceptual frameworks can be developed and also replaced
by new, better ones; it is we who create our ‘prisons’ and we can also,
critically, demolish them.?

New steps from conservative to revolutionary activism were made by
Whewell and then by Poincaré, Milhaud and Le Roy. Whewell held
that theories are developed by trial and error—in the ‘preludes to the in-
ductive epochs’. The best ones among them are then ‘proved’—during the
‘inductive epochs’—by a long primarily a priori consideration which he
called ‘progressive intuition’. The ‘inductive epochs’ are followed by
‘sequels to the inductive epochs’: cumulative developments of auxiliary
theories.* Poincaré, Milhaud and Le Roy were averse to the idea of proof by
progressive intuition and preferred to explain the continuing historical
success of Newtonian mechanics by a methodological decision taken by
scientists: after a considerable period of initial empirical success scientists

1This demarcation—and terminology—is due to Popper; ef. especially his [1934],
section 19 and his [1945], chapter 23 and footnote 3 to chapter 25.

2No version of conservative activism explained why Newton’s gravitational theory
should be invulnerable; Kantians restricted themselves to the explanation of the tenacity
of Euclidean geometry and Newtonian mechanics. About Newtonian gravitation and optics
(or other branches of science) they had an ambiguous, and occasionally inductivist position.

3 IT do not include Hegel among ‘revolutionary activists’, For Hegel and his followers
change in conceptual frameworks is a predetermined, inevitable process, where individual
creativity or rational criticism plays no essential role. Those who run ahead are equally at
fault as those who stay behind in this ‘dialectic’. The clever man is not he who creates a
better ‘prison’ or who demolishes critically the old one, but the one who is always in
step with history. Thus dialectic accounts for change without criticism.

4Cf. Whewell’s [1837], [1840] and [1858].

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 105

may decide not to allow the theory to be refuted. Once they have taken this
decision, they solve (or dissolve) the apparent anomalies by auxiliary
hypotheses or other ‘conventionalist stratagems.’! This conservative con-
ventionalism has, however, the disadvantage of making us unable to get out
of our self-imposed prisons, once the first period of trial-and-error is over
and the great decision taken. It cannot solve the problem of the elimina-
tion of those theories which have been triumphant for a long period.
According to conservative conventionalism, experiments may have suffi-
cient power to refute young theories, but not to refute old, established
theories: as science grows, the power of empirical evidence diminishes.”

Poincaré’s critics refused to accept his idea, that, although the scientists
build their conceptual frameworks, there comes a time when these frame-
works turn into prisons which cannot be demolished. This criticism gave
rise to two rival schools of revolutionary conventionalism: Duhem’s sim-
plicism and Popper’s methodological falsificationism.®

Duhem accepts the conventionalists’ position that no physical theory
ever crumbles merely under the weight of ‘refutations’, but claims that it
still may crumble under the weight of ‘continual repairs, and many
tangled-up stays’ when ‘the worm-eaten columns’ cannot support ‘the
tottering building’ any longer‘; then the theory loses its original simplicity
and has to be replaced. But falsification is then left to subjective taste or,
at best, to scientific fashion, and leaves too much leeway for dogmatic
adherence to a favourite theory.5

Popper set out to find a criterion which is both more objective and more

1 Cf. especially Poincaré [1891] and [1902]; Milhaud [1896]; Le Roy [1899] and [1901].
It was one of the chief philosophical merits of conventionalists to direct the limelight to
the fact that any theory can be saved by ‘conventionalist stratagems’ from refutations.
(The term ‘conventionalist stratagem’ is Popper’s; cf. the critical discussion of Poincaré’s
conventionalism in his [1934], especially sections 19 and 20.)

® Poincaré first elaborated his conventionalism only with regard to geometry (cf. his
[1891]). Then Milhaud and Le Roy generalized Poincaré’s idea to cover all branches of
accepted physical theory. Poincaré’s [1902] starts with a strong criticism of the Bergsonian
Le Roy against whom he defends the empirical (falsifiable or ‘inductive’) character of
all physics except for geometry and mechanics. Duhem, in turn, criticized Poincaré: in his
view there was a possibility of overthrowing even Newtonian mechanics.

3 The loci classici are Duhem’s [1905] and Popper’s [1934]. Duhem was not a consistent
revolutionary conventionalist. Very much like Whewell, he thought that conceptual
changes are only preliminaries to the final—if perhaps distant—‘natural classification’:
‘The more a theory is perfected, the more we apprehend that the logical order in which
it arranges experimental laws is the reflection of an ontological order,’ In particular, he
refused to see Newton’s mechanics actually ‘crumbling’ and characterized Einstein’s
relativity theory as the manifestation of a ‘frantic and hectic race in pursuit of a novel
idea’ which ‘has turned physics into a real chaos where logic loses its way and common-
sense runs away frightened’ (Preface—of 1914—to the second edition of his [1905)]).

4 Duhem [1905], chapter VI, section 10.
5 For a further discussion of conventionalism, cf. below, pp. 184-189.

106 IMRE LAKATOS

hard-hitting. He could not accept the emasculation of empiricism, in-
herent even in Duhem’s approach, and proposed a methodology which
allows experiments to be powerful even in ‘mature’ science. Popper’s
methodological falsificationism is both conventionalist and falsificationist,
but he ‘differs from the [conservative] conventionalists in holding that the
statements decided by agreement are vot [spatio-temporally] universal but
[spatio-temporally] singular’; and he differs from the dogmatic falsifica-
tionist in holding that the truth-value of such statements cannot be proved
by facts but, in some cases, may be decided by agreement.?

The conservative conventionalist (or methodological justificationist, if
you wish) makes unfalsifiable by fiat some (spatio-temporally) universal
theories, which are distinguished by their explanatory power, simplicity or
beauty. Our revolutionary conventionalist (or ‘methodological falsificationist’)
makes unfalsifiable by fiat some (spatio-temporally) singular statements
which are distinguishable by the fact that there exists at the time a ‘relevant
technique’ such that ‘anyone who has learned it’ will be able to decide that
the statement is ‘acceptable’? Such a statement may be called an ‘observa-
tional’ or ‘basic’ statement, but only in inverted commas.* Indeed, the
very selection of all such statements is a matter of a decision, which is not
based on exclusively psychological considerations. This decision is then
followed by a second kind of decision concerning the separation of the set
of accepted basic statements from the rest.

These two decisions correspond to the two assumptions of dogmatic falsi-
ficationism. But there are important differences. First, the methodological
falsificationist is not a justificationist, he has no illusions about ‘experi-
mental proofs’ and is fully aware of the fallibility of his decisions and the
risks he is taking.

The methodological falsificationist realizes that in the ‘experimental
techniques’ of the scientist fallible theories are involved,® ‘in the light of
which’ he interprets the facts. In spite of this he ‘applies’ these theories,
he regards them in the given context not as theories under test but as
unproblematic background knowledge ‘which we accept (tentatively) as
unproblematic while we are testing the theory’.® He may call these theories
~—and the statements whose truth-value he decides in their light—‘obser-

Popper [1934], section 30,

2 In this section I discuss the ‘naive’ variant of Popper’s methodological falsificationism.
Thus, throughout the section ‘methodological falsificationism’ stands for ‘naive methodological
falsificationism ; for this ‘naivety’, cf. below, pp. 115-116.

3 Popper [1934], section 27,

‘ Op. cit. section 28. For the non-basicness of these methodologically ‘basic’ statements,
cf. e.g. Popper [1934] passim and Popper [19594], p. 35, footnote *2.

*> Cf. Popper [1934], end of section 26 and also his [1968c], pp. 291-2.

® Cf. Popper [1963], p. 390.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 107

vational’: but this is only a manner of speech which he inherited from
naturalistic falsificationism.! The methodological falsificationist uses our
most successful theories as extensions of our senses and widens the range of
theories which can be applied in testing far beyond the dogmatic falsifi-
cationist’s range of strictly observational theories. For instance, let us
imagine that a big radio-star is discovered with a system of radio-star
satellites orbiting it. We should like to test some gravitational theory on this
planetary system—a matter of considerable interest. Now let us imagine
that Jodrell Bank succeeds in providing a set of space-time co-ordinates of
the planets which is inconsistent with the theory. We shall take these
statements as potential falsifiers. Of course, these basic statements are not
‘observational’ in the usual sense but only “ ‘observational’ ”’. They
describe planets that neither the human eye nor optical instruments can
reach. Their truth-value is arrived at by an ‘experimental technique’. This
‘experimental technique’ is based on the ‘application’ of a well-corroborated
theory of radio-optics. Calling these statements ‘observational’ is no more
than a manner of saying that, in the context of his problem, that is, in
testing our gravitational theory, the methodological falsificationist uses
radio-optics uncritically, as ‘background knowledge’. The need for decisions
to demarcate the theory under test from unproblematic background knowledge
is a characteristic feature of this brand of methodological falsificationism.”
(This situation does not really differ from Galileo’s ‘observation’ of
Jupiter’s satellites: moreover, as some of Galileo’s contemporaries rightly
pointed out, he relied on a virtually non-existent optical theory—which
then was less corroborated, and even less articulated, than present-day
radio-optics. On the other hand, calling the reports of our human eye
‘observational’ only indicates that we ‘rely’ on some vague physiological
theory of human vision.*)

This consideration shows the conventional element in granting—in a
given context—the (methodologically) ‘observational’ status to a theory.‘
Similarly, there is a considerable conventional element in the decision
concerning the actual truth-value of a basic statement which we take after
we have decided which ‘observational theory’ to apply. One single observa-
tion may be the stray result of some trivial error: in order to reduce
such risks, methodological falsificationists prescribe some safety control.
The simplest such control is to repeat the experiment (it is a matter of

1 Indeed, Popper carefully puts ‘observational’ in quotes; cf. his [1934], section 28,

2 This demarcation plays a role both in the first and in the fourth type of decisions of
the methodological falsificationist. (For the fourth decision, cf. below, p. 110.)

3 For a fascinating discussion, cf. Feyerabend [1969].

# One wonders whether it would not be better to make a break with the terminology of
naturalistic falsificationism and rechristen observational theories ‘touchstone theories’.

108 IMRE LAKATOS

convention how many times); another is to ‘fortify’ the potential falsifier
by a ‘well-corroborated falsifying hypothesis’.

The methodological falsificationist also points out that, as a matter of
fact, these conventions are institutionalized and endorsed by the scientific
community; the list of ‘accepted’ falsifiers is provided by the verdict of the
experimental scientists.”

This is how the methodological falsificationist establishes his ‘empirical
basis’. (He uses inverted commas in order ‘to give ironical emphasis’ to the
term.*) This ‘basis’ can be hardly called a ‘basis’ by justificationist stan-
dards: there is nothing proven about it—it denotes ‘piles driven into a
swamp’.* Indeed, if this ‘empirical basis’ clashes with a theory, the theory
may be called ‘falsified’, but it is not falsified in the sense that it is disproved.
Methodological ‘falsification’ is very different from dogmatic falsification.
If a theory is falsified, it is proven false; if it is ‘falsified’, it may still be
true. If we follow up this sort of ‘falsification’ by the actual ‘elimination’ of
a theory, we may well end up by eliminating a true, and accepting a false,
theory (a possibility which is thoroughly abhorrent to the old-fashioned
justificationist).

Yet the methodological falsificationist advises that exactly this is to be
done. The methodological falsificationist realizes that if we want to recon-
cile fallibilism with (non-justificationist) rationality, we must find a way to
eliminate some theories. If we do not succeed, the growth of science will be
nothing but growing chaos.

Therefore the methodological falsificationist maintains that ‘[if we want]
to make the method of selection by elimination work, and to ensure that
only the fittest theories survive, their struggle for life must be made
severe’.5 Once a theory has been falsified, in spite of the risk involved, it
must be eliminated: ‘[with theories we work only] as long as they stand up
to tests’.6 The elimination must be methodologically conclusive: ‘In gen-
eral we regard an inter-subjectively testable falsification as final...A
corroborative appraisal made at a later date...can replace a positive
degree of corroboration by a negative one, but not vice versa’.’ This is the

1 Cf. Popper [1934], section 22. Many philosophers overlooked Popper’s important
qualification that a basic-statement has no power to refute anything without the support
of a well-corroborated falsifying hypothesis.

2 Cf. Popper [1934], section 30.

* Popper [1963], p. 387.

4 Popper [1934], section 30; also cf. section 29: “The Relativity of Basic Statements.’

§ Popper [1957], p. 134 Popper, in other places, emphasizes that his method cannot
‘ensure’ the survival of the fittest. Natural selection may go wrong: the fittest may perish
and monsters survive.

* Popper [1935].

? Popper [7934], section 82.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES Iog

methodological falsificationist’s explanation of how we get out of a rut: ‘It
is always the experiment which saves us from following a track that leads
nowhere.”!

The methodological falsificationist separates rejection and disproof, which
the dogmatic falsificationist had conflated.? He is a fallibilist but his falli-
bilism does not weaken his critical stance: he turns fallible propositions into
a ‘basis’ for a hard-line policy. On these grounds he proposes a mew demarca-
tion criterion: only those theories—that is, non-‘observational’ propositions
—which forbid certain ‘observable’ states of affairs, and therefore may be
‘falsified’ and rejected, are ‘scientific’: or, briefly, a theory 1s ‘scientific’ (or
‘acceptable’) if it has an ‘empirical basis’. This eriterion brings out sharply
the difference between dogmatic and methodological falsificationism.®

This methodological demarcation criterion is much more liberal than
the dogmatic one. Methodological falsificationism opens up new avenues of
criticism: many more theories may qualify as ‘scientific’. We have already
seen that there are more ‘observational’ theories than observational
theories,* and therefore there are more ‘basic’ statements than basic
statements.’ Furthermore, probabilistic theories may qualify now as
‘scientific’: although they are not falsifiable they can be easily made
‘falsifiable’ by an additional (third type) decision which the scientist can
make by specifying certain rejection rules which may make statistically
interpreted evidence ‘inconsistent’ with the probabilistic theory.®

1 Popper [1934], section 82.

2 This kind of methodological ‘falsification’ is, unlike dogmatic falsification (disproof),
a pragmatic, methodological idea. But then what exactly should we mean by it? Popper’s
answer—which I am going to discard—is that methodological ‘falsification’ indicates an
‘urgent need of replacing a falsified hypothesis by a better one’ (Popper [1959], p. 87,
footnote *1). This shift is an excellent illustration of the process I described in my [1963-4]
whereby critical discussion shifts the original problem without necessarily changing the
old terms, The byproducts of such processes are meaning-shifts. For a further discussion,
cf. below, p. 122, footnote 4, and p. 157, footnote 1.

3 The demarcation criterion of the dogmatic falsificationist was: a theory is ‘scientific’
if it has an empirical basis (see above, p. 98).

* See above, pp. 98-9.

5 Incidentally, Popper, in his [r934], does not seem to have seen this point clearly.
He writes: ‘Admittedly, it is possible to interpret the concept of an observable event in a
psychologistic sense. But I am using it in such a sense that it might just as well be replaced
by “an event involving position and movement of macroscopic physical bodies”’ ’. ([1934],
section 28.) In the light of our discussion, for instance, we may regard a positron passing
through a Wilson chamber at time ¢) as an ‘observable’ event, in spite of the non-macro-
scopic character of the positron.

® Popper [1934], section 68. Indeed, this methodological falsificationism is the philo-
sophical basis of some of the most interesting developments in modern statistics. The
Neyman-Pearson approach rests completely on methodological falsificationism. Also
cf, Braithwaite [1953], chapter VI. (Unfortunately, Braithwaite reinterprets Popper’s
demarcation criterion as separating meaningful from meaningless rather than scientific
from non-scientific propositions.)

Ilo IMRE LAKATOS

But even these three decisions are not sufficient to enable us to ‘falsify’
a theory which cannot explain anything ‘observable’ without a ceteris
paribus clause.1 No finite number of ‘observations’ is enough to ‘falsify’
such a theory. However, if this is the case how can one reasonably de-
fend a methodology which claims to ‘interpret natural laws or theories
as... Statements which are partially decidable, i.e. which are, for logical
reasons, not verifiable but, in an asymmetrical way, falsifiable . . .’?? How
can we interpret theories like Newton’s theory of dynamics and gravi-
tation as ‘one-sidedly decidable’? How can we make in such cases genuine
‘attempts to weed out false theories—to find the weak points of a theory in
order to reject it if it is falsified by the test’?# How can we draw them into
the realm of rational discussion? The methodological falsificationist solves
the problem by making a further (fourth type) decision: when he tests a
theory together with a ceteris paribus clause and finds that this conjunction
has been refuted, he must decide whether to take the refutation also as a
refutation of the specific theory. For instance, he may accept Mercury’s
‘anomalous’ perihelion as a refutation of the treble conjunction N, of
Newton’s theory, the known initial conditions and the ceteris paribus
clause. Then he tests the initial conditions ‘severely’® and may decide to
relegate them into the ‘unproblematic background knowledge’. This
decision implies the refutation of the double conjunction N, of Newton’s
theory and the ceteris paribus clause. Now he has to take the crucial de-
cision: whether to relegate also the ceteris paribus clause into the pool of
‘unproblematic background knowledge’. He will do so if he finds the
ceteris paribus clause well corroborated.

How can one test a ceteris paribus clause severely? By assuming that there
are other influencing factors, by specifying such factors, and by testing
these specific assumptions. If many of them are refuted, the ceteris paribus
clause will be regarded as well-corroborated.

Yet the decision to ‘accept’ a ceteris paribus clause is a very risky one
because of the grave consequences it implies. If it is decided to accept it as
part of such background knowledge, the statements describing Mercury’s
perihelion from the empirical basis of N, are turned into the empirical basis
of Newton’s specific theory N, and what was previously a mere ‘anomaly’ in
relation to N,, becomes now crucial evidence against it, its falsification.
(We may call an event described by a statement A an ‘anomaly in relation
to a theory 7” if A is a potential falsifier of the conjunction of T and a
ceteris paribus clause but it becomes a potential falsifier of T itself after

1 Cf. above, pp. 101-3.

* Popper [1933]- * Popper [1933]. * Popper [1957], p. 133.

5 For a discussion of this important concept of Popperian methodology, cf. my [1968a],
Pp. 397 ff.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES III

having decided to relegate the ceteris paribus clause into ‘unproblematic
background knowledge.’!) Since, for our savage falsificationist, falsifica-
tions are methodologically conclusive,? the fateful decision amounts to the
methodological elimination of Newton’s theory, making further work on it
irrational. If the scientist shrinks back from such bold decisions he will
‘never benefit from experience’, ‘believing, perhaps, that it is his business
to defend a successful system against criticism as long as it is not con-
clusively disproved’.? He will degenerate into an apologist who may always
claim that ‘the discrepancies which are asserted to exist between the experi-
mental results and the theory are only apparent and that they will dis-
appear with the advance of our understanding’.* But for the falsificationist
this is ‘the very reverse of the critical attitude which is the proper one for
the scientist’,> and is impermissible. To use one of the methodological
falsificationist’s favourite expressions: the theory ‘must be made to stick
its neck out’.

The methodological falsificationist is in a serious plight when it comes to
deciding where to draw the demarcation, even if only in a well-defined
context, between the problematic and unproblematic. The plight is most
dramatic when he has to make a decision about ceteris paribus clauses, when
he has to promote one of the hundreds of ‘anomalous phenomena’ into a
‘crucial experiment’, and decide that in such a case the experiment was

‘controlled’.®
Thus, with the help of this fourth type of decision,’ our methodological

falsificationist has finally succeeded in interpreting even theories like
Newton’s theory as ‘scientific’.®

1 For an improved ‘explication’, cf. below, p. 159, footnote 1.

2 Cf. above, p. 108, text to footnotes 6 and 7.

3 Popper [1934], section 9.

* Ibid. 5 Ibid.

6 The problem of ‘controlled experiment’ may be said to be nothing else but the problem
of arranging experimental conditions in such a way as to minimize the risk involved in
such decisions.

? This type of decision belongs, in an important sense, to the same category as the
first decision: it demarcates, by decision, problematic from unproblematic knowledge.
Cf. above, p. 107, text to footnote 2.

® Our exposition shows clearly the complexity of the decisions needed to define the
‘empirical content’ of a theory—that is, the set of its potential falsifiers. ‘Empirical
content’ depends on our decision as to which are our ‘observational theories’ and which
anomalies are to be promoted to counterexamples. If one attempts to compare the empirical
content of different scientific theories in order to see which is ‘more scientific’, then one
will get involved in an enormously complex and therefore hopelessly arbitrary system of
decisions about their respective classes of ‘relatively atomic statements’ and their ‘fields
of application’. (For the meaning of these (very) technical terms, cf. Popper [1934],
section 38.) But such comparison is possible only when one theory supersedes another (cf.
Popper, [1959a], p. 401, footnote 7). And even then, there may be difficulties (which
would not, however, add up to irremediable ‘incommensurability’),

112 IMRE LAKATOS

Indeed, there is no reason why he should not go yet another step. Why
not decide that a theory—which even these four decisions cannot turn into
an empirically falsifiable one—is falsified if it clashes with another theory
which is scientific on some of the previously specified grounds and is also
well-corroborated?! After all, if wereject one theory because one of its poten-
tial falsifiers is seen to be true in the light of an observational theory, why
not reject another theory because it clashes directly with one that may be
relegated into unproblematic background knowledge? This would allow
us, by a fifth type decision, to eliminate even ‘syntactically metaphysical’
theories, that is, theories, which, like ‘all-some’ statements or purely
existential statements,” because of their logical form cannot have spatio-
temporally singular potential falsifiers.

To sum up: the methodological falsificationist offers an interesting
solution to the problem of combining hard-hitting criticism with falli-
bilism. Not only does he offer a philosophical basis for falsification after
fallibilism had pulled the carpet from under the feet of the dogmatic
falsificationist, but he also widens the range of such criticism very con-
siderably. By putting falsification in a new setting, he saves the attractive
code of honour of the dogmatic falsificationist: that scientific honesty
consists in specifying, in advance, an experiment such, that if the result
contradicts the theory, the theory has to be given up.®

Methodological falsificationism represents a considerable advance
beyond both dogmatic falsificationism and conservative conventionalism.
It recommends risky decisions. But the risks are daring to the point of
recklessness and one wonders whether there is no way of lessening them.

Let us first have a closer look at the risks involved.

Decisions play a crucial role in this methodology—as in any brand of
conventionalism. Decisions however may lead us disastrously astray. The
methodological falsificationist is the first to admit this. But this, he argues,
is the price which we have to pay for the possibility of progress.

One has to appreciate the dare-devil attitude of our methodological
falsificationist. He feels himself to be a hero who, faced with two catas-
trophic alternatives, dared to reflect coolly on their relative merits and
choose the lesser evil. One of the alternatives was sceptical fallibilism, with
its ‘anything goes’ attitude, the despairing abandonment of all intellectual
standards, and hence of the idea of scientific progress. Nothing can be
established, nothing can be rejected, nothing even communicated: the

1 This was suggested by J. O. Wisdom: cf. his [1963].

2 For instance: ‘All metals have a solvent’; or ‘There exists a substance which can turn
all metals into gold’, For discussions of such theories, cf. especially Watkins [1957]
and Watkins [1960]. But cf. below, pp. 126-7 and pp. 183-4.

5 See above, p. 96.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES I113

growth of science is a growth of chaos, a veritable Babel. For two thousand
years, scientists and scientifically-minded philosophers chose justifica-
tionist illusions of some kind to escape this nightmare. Some of them
argued that one has to choose between inductivist justificationism and irrat-
ionalism: ‘T do not see any way out of a dogmatic assertion that we know the
inductive principle or some equivalent; the only alternative is to throw over
almost everything that is regarded as knowledge by science and common
sense.’ Our methodological falsificationist proudly rejects such escapism:
he dares to measure up to the full impact of fallibilism and yet escape
scepticism by a daring and risky conventionalist policy, with no dogmas.
He is fully aware of the risks but insists that one has to choose between some
sort of methodological falsificationism and trrationalism. He offers a game in
which one has little hope of winning, but claims that it is still better to
play than to give up.”

Indeed, those critics of naive falsificationism who offer no alternative
method of criticism are inevitably driven to irrationalism. For instance,
Neurath’s muddled argument, that the falsification and ensuing elimina-
tion of a hypothesis may turn out to have been ‘an obstacle in the progress
of science’,® carries no weight as long as the only alternative he seems to
offer is chaos. Hempel is, no doubt, right in stressing that ‘science offers
various examples [when] a conflict between a highly-confirmed theory and
an occasional recalcitrant experiential sentence may well be resolved by
revoking the latter rather than by sacrificing the former’*; nevertheless he
admits that he can offer no other ‘fundamental standard’ than that of
naive falsificationism.’ Neurath—and, seemingly, Hempel—reject falsi-
ficationism as ‘pseudo-rationalism’®; but where is ‘real rationalism’?
Popper warned already in 1934 that Neurath’s permissive methodology (or
rather lack of methodology) would make science unempirical and therefore

2 Russell [1943], p. 683.

2 I am sure that some will welcome methodological falsificationism as an ‘existentialist’
philosophy of science.

3 Neurath [1935], p- 356.

4 Hempel [1952], p. 621. Agassi, in his [1966], follows Neurath and Hempel, especially
pp. 16 ff. It is rather amusing that Agassi, in making this point, thinks that he is taking
up arms against ‘the whole literature concerning the methods of science’.

Indeed, many scientists were fully aware of the difficulties inherent in the ‘confrontation
of theory and facts’. (Cf. Einstein [1949], p. 27-) Several philosophers sympathetic to
falsificationism emphasized that ‘the process of refuting a scientific hypothesis is more
complicated than it appears to be at first sight’ (Braithwaite [1953], p. 20). But only
Popper offered a constructive, rational solution.

5 Hempel [1952], p. 622. Hempel’s crisp ‘theses on empirical certainty’ do nothing but
refurbish Neurath’s—and some of Popper’s—old arguments (against Carnap, I take it);
but deplorably, he does not mention either his predecessors or his adversaries.

6 Neurath [1935].

II4 IMRE LAKATOS

irrational: ‘We need a set of rules to limit the arbitrariness of “deleting” (or
else “‘accepting”’) a protocol sentence. Neurath fails to give any such rules
and thus unwittingly throws empiricism overboard... Every system
becomes defensible if one is allowed (as everybody is, in Neurath’s view)
simply to “delete’’ a protocol sentence if it is inconvenient’.1 Popper agrees
with Neurath that all propositions are fallible; but he forcefully makes the
crucial point that we cannot make progress unless we have a firm rational
strategy or method to guide us when they clash.?

But is not the firm strategy of the brand of methodological falsifica-
tionism hitherto discussed too firm? Are not the decisions it advocates
bound to be too arbitrary? Some may even claim that all that distinguishes
methodological from dogmatic falsificationism is that zt pays lip-service to
fallibilism!

To criticize a theory of criticism is usually very difficult. Naturalistic
falsificationism was relatively easy to refute, since it rested on an empirical
psychology of perception: one could show that it was simply false. But
how can methodological falsificationism be falsified? No disaster can ever
disprove a non-justificationist theory of rationality. Moreover, how can we
ever recognize an epistemological disaster? We have no means to judge
whether the verisimilitude of our successive theories increases or de-
creases.3 At this stage we have not yet developed a general theory of
criticism even for scientific theories, let alone for theories of rationality?:
therefore if we want to falsify our methodological falsificationism, we have
to do it before having a theory of how to do it.

If we look at history of science, if we try to see how some of the most
celebrated falsifications happened, we have to come to the conclusion that
either some of them are plainly irrational, or that they rest on rationality
principles radically different from the ones we just discussed. First of all,
our falsificationist must deplore the fact that stubborn theoreticians fre-
quently challenge experimental verdicts and have them reversed. In the
falsificationist conception of scientific ‘law and order’ we have described
there is no place for such successful appeals. Further difficulties arise from
the falsification of theories to which a ceteris paribus clause is appended.®

1 Popper [1934], section 26.

® Neurath’s [1935] shows that he never grasped Popper’s simple argument.

3 1 am using here ‘verisimilitude’ in Popper’s sense: the difference between the truth

content and falsity content of a theory. For the risks involved in estimating it, cf. my
(1968a], especially pp. 395 ff.

“I tried to develop such a general theory of criticism in my [1970].

5 The falsification of theories depends on the high degree of corroboration of the
ceteris paribus clause. This however is not always the case. This is why the methodological
falsificationist may advise us to rely on our ‘scientific instinct’ (Popper [1934], section 18,
footnote 2) or ‘hunch’ (Braithwaite [1953], p. 20).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES I15§

Their falsification as it occurs in actual history is prima facie irrational by
the standards of our falsificationist. By his standards, scientists frequently
seem to be irrationally slow: for instance, eighty-five years elapsed between
the acceptance of the perihelion of Mercury as an anomaly and its accept~
ance as a falsification of Newton’s theory, in spite of the fact that the ceteris
paribus clause was reasonably well corroborated. On the other hand,
scientists frequently seem to be irrationally rash: for instance, Galileo and
his disciples accepted Copernican heliocentric celestial mechanics in spite
of the abundant evidence against the rotation of the Earth; or Bohr and
his disciples accepted a theory of light emission in spite of the fact that
it ran counter to Maxwell’s well-corroborated theory.

Indeed, it is not difficult to see at least two crucial characteristics
common to both dogmatic and our methodological falsificationism which are
clearly dissonant with the actual history of science: that (1) @ test is—or
must be made—a two-cornered fight between theory and experiment so that in
the final confrontation only these two face each other; and (2) the only inter-
esting outcome of such confrontation is (conclusive) falsification: ‘[the only
genuine] discoveries are refutations of scientific hypotheses.’ However,
history of science suggests that (1’) tests are—at least—three-cornered
fights between rival theories and experiment and (2') some of the most
interesting experiments result, prima facie, in confirmation rather than
falsification.

But if—as seems to be the case—the history of science does not bear
out our theory of scientific rationality, we have two alternatives. One
alternative is to abandon efforts to give a rational explanation of the success
of science. Scientific method (or ‘logic of discovery’), conceived as the
discipline of rational appraisal of scientific theories—and of criteria of
progress—vanishes. We, may, of course, still try to explain changes in
‘paradigms’ in terms of social psychology.? This is Polanyi’s and Kuhn’s
way.? The other alternative is to try at least to reduce the conventional
element in falsificationism (we cannot possibly eliminate it) and replace the

1 Agassi [1959]; he calls Popper’s idea of science ‘scientia negativa’ (Agassi [1968]).

2 It should be mentioned here that the Kuhnian sceptic is still left with what I would
call the ‘scientific sceptic’s dilemma’: any scientific sceptic will still try to explain changes in
beliefs and will regard his own psychology as a theory which is more than simple belief,
which, in some sense, is ‘scientific’. Hume, while trying to show up science as a mere
system of beliefs with the help of his stimulus-response theory of learning, never raised
the problem of whether his theory of learning applies also to his own theory of learning.
In contemporary terms, we might well ask, does the popularity of Kuhn’s philosophy
indicate that people recognize its truth? In this case it would be refuted. Or does this
popularity indicate that people regarded it as an attractive new fashion? In this case, it
would be ‘verified’. But would Kuhn like this ‘verification’?

3 Feyerabend who contributed probably more than anybody else to the spread of
Popper’s ideas, seems now to have joined the enemy camp. Cf. his intriguing [1970].

116 IMRE LAKATOS

naive versions of methodological falsificationism—characterized by the
theses (1) and (2) above—by a sophisticated version which would give a new
rationale of falsification and thereby rescue methodology and the idea of
scientific progress. This is Popper’s way, and the one I intend to follow.

Sophisticated falsificationism differs from naive falsificationism both in
its rules of acceptance (or ‘demarcation criterion’) and its rules of falsifi-
cation or elimination. For the naive falsificationist any theory which can be
interpreted as experimentally falsifiable, is ‘acceptable’ or ‘scientific’.! For
the sophisticated falsificationist a theory is ‘acceptable’ or ‘scientific’ only
if it has corroborated excess empirical content over its predecessor (or
rival), that is, only if it leads to the discovery of novel facts. This condition
can be analysed into two clauses: that the new theory has excess em-
pirical content (‘acceptability’,) and that some of this excess content is
verified (‘acceptability’,). The first clause can be checked instantly? by a
priori logical analysis; the second can be checked only empirically and
this may take an indefinite time.

Again, for the naive falsificationist a theory is falsified by a ‘(fortified’)
‘observational’ statement which conflicts with it (or rather, which he
decides to interpret as conflicting with it). The sophisticated falsifica-
tionist regards a scientific theory 7 as falsified if and only if another theory
T’ has been proposed with the following characteristics: (1) T’ has excess
empirical content over T: that is, it predicts movel facts, that is, facts
improbable in the light of, or even forbidden, by 7;4 (2) T’ explains the
previous success of T, that is, all the unrefuted content of T is contained
(within the limits of observational error) in the content of T’; and (3) some
of the excess content of T’ is corroborated.5

In order to beable to appraise these definitions we need to understand their
problem background and their consequences. First, we have to remember
the conventionalists’ methodological discovery that no experimental result
can ever kill a theory: any theory can be saved from counterinstances
either by some auxiliary hypothesis or by a suitable reinterpretation of its
terms. Naive falsificationists solved this problem by relegating—in crucial
contexts—the auxiliary hypotheses to the realm of unproblematic back-
ground knowledge, eliminating them from the deductive model of the test-

1Cf£. above, p. 109. ? But ef. below, pp. 155-7. * Cf. above, p. 108, text to footnote 1.

4T use ‘prediction’ in a wide sense that includes ‘postdiction’.

5 For a detailed discussion of these acceptance and rejection rules and for references to

Popper’s work, cf. my [1968a], pp. 375-90. For some qualifications (concerning continuity
and consistency as regulative principles), cf. below, pp. 131-2 and 141-6.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 117

situation and thereby forcing the chosen theory into logical isolation, in
which it becomesa sitting target for the attack of test-experiments. But since
this procedure did not offer a suitable guide for a rational reconstruction of
the history of science, we may just as well completely rethink our approach.
Why aim at falsification at any price? Why not rather impose certain
standards on the theoretical adjustments by which one is allowed to save a
theory? Indeed, some such standards have been well-known for centuries,
and we find them expressed in age-old wisecracks against ad hoc explana-
tions, empty prevarications, face-saving, linguistic tricks.1 We have already
seen that Duhem adumbrated such standards in terms of ‘simplicity’ and
‘good sense’.? But when does lack of ‘simplicity’ in the protective belt of
theoretical adjustments reach the point at which the theory must be
abandoned?’ In what sense was Copernican theory, for instance, ‘simpler’
than Ptolemaic? The vague notion of Duhemian ‘simplicity’ leaves, as the
naive falsificationist correctly argued, the decision very much to taste and
fashion.®

Can one improve on Duhem’s approach? Popper did. His solution—a
sophisticated version of methodological falsificationism—is more objective
and more rigorous. Popper agrees with the conventionalists that theories
and factual propositions can always be harmonized with the help of aux-
iliary hypotheses: he agrees that the problem is how to demarcate between
scientific and pseudoscientific adjustments, between rational and irrational
changes of theory. According to Popper, saving a theory with the help of
auxiliary hypotheses which satisfy certain well-defined conditions re-
presents scientific progress; but saving a theory with the help of auxiliary
hypotheses which do not, represents degeneration. Popper calls such
inadmissible auxiliary hypotheses ad hoc hypotheses, mere linguistic
devices, ‘conventionalist stratagems’. But then any scientific theory has to

1 Moliére, for instance, ridiculed the doctors of his Malade Imaginaire, who offered the
virtus dormitiva of opium as the answer to the question as to why opium produced sleep.
One might even argue that Newton’s famous dictum hypotheses non fingo was really
directed against ad hoc explanations—like his own explanation of gravitational forces
by an aether-model in order to meet Cartesian objections. 2 Cf. above, p. 105.

8 Incidentally, Duhem agreed with Bernard that experiments alone—without sim-
plicity considerations—can decide the fate of theories in physiology. But in physics, he
argued, they cannot ([1905], chapter VI, section 1).

* Koestler correctly points out that only Galileo created the myth that the Copernican
theory was simple (Koestler [1959], p. 476); in fact, ‘the motion of the earth [had not]
done much to simplify the old theories, for though the objectionable equants had dis-
appeared, the system was still bristling with auxiliary circles’ (Dreyer [1906], chapter
XIII). 5 Cf. above, p. 105.

® Popper [1934], sections 19 and 20. I have discussed in some detail—under the heads

‘monster-barring’, ‘exception-barring’, ‘monster-adjustment’—such stratagems as they
appear in informal, quasi-empirical mathematics; cf. my [1963-4].

118 IMRE LAKATOS

be appraised together with its auxiliary hypotheses, initial conditions, etc.,
and, especially, together with its predecessors so that we may see by what
sort of change it was brought about. Then, of course, what we appraise is a
series of theories rather than isolated theories.

Now we can easily understand why we formulated the criteria of accept-
ance and rejection of sophisticated methodological falsificationism as we
did.! But it may be worth while to reformulate them slightly, couching
them explicitly in terms of series of theories.

Let us take a series of theories, T,, 7, 7'3,... where each subsequent
theory results from adding auxiliary clauses to (or from semantical re-
interpretations of) the previous theory in order to accommodate some
anomaly, each theory having at least as much content as the unrefuted
content of its predecessor. Let us say that such a series of theories is
theoretically progressive (or ‘constitutes a theoretically progressive problem-
shift’) if each new theory has some excess empirical content over its pre-
decessor, that is, if it predicts some novel, hitherto unexpected fact. Let us
say that a theoretically progressive series of theories is also empirically
progressive (or ‘constitutes an empirically progressive problemshift’) if some of
this excess empirical content is also corroborated, that is, if each new theory
leads us to the actual discovery of some new fact.? Finally, let us call a
problemshift progressive if it is both theoretically and empirically pro-
gressive, and degenerating if it is not.* We ‘accept’ problemshifts as ‘scien-
tific’ only if they are at least theoretically progressive; if they are not, we
‘reject’ them as ‘pseudoscientific’. Progress is measured by the degree to
which a problemshift is progressive, by the degree to which the series of
theories leads us to the discovery of novel facts. We regard a theory in the
series ‘falsified’ when it is superseded by a theory with higher corroborated
content.‘

This demarcation between progressive and degenerating problemshifts
sheds new light on the appraisal of scientific—or, rather, progressive—

1 Cf. above, p. 116.

21f I already know P,: ‘Swan A is white’, Pw: ‘All swans are white’ represents no
progress, because it may only lead to the discovery of such further similar facts as P2:
‘Swan B is white’. So-called ‘empirical generalizations’ constitute no progress. A mew
fact must be improbable or even impossible in the light of previous knowledge. Cf. above,
p. 116, and below, pp. 155 ff.

3 The appropriateness of the term ‘problemshift’ for a series of theories rather than
of problems may be questioned. I chose it partly because I have not found a more appro-
priate alternative—‘theoryshift’ sounds dreadful—partly because theories are always
problematical, they never solve all the problems they have set out to solve. Anyway, in
the second half of the paper, the more natural term ‘research programme’ will replace
‘problemshifts’ in the most relevant contexts.

‘For the ‘falsification’ of certain series of theories (of ‘research programmes’) as
opposed to the ‘falsification’ of one theory within the series, cf. below, pp. 155 ff.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 119

explanations. If we put forward a theory to resolve a contradiction between
a previous theory and a counterexample in such a way that the new theory,
instead of offering a content-increasing (scientific) explanation, only offers a
content-decreasing (linguistic) reinterpretation, the contradiction is re-
solved in a merely semantical, unscientific way. A given fact is explained
scientifically only if a new fact is also explained with it.

Sophisticated falsificationism thus shifts the problem of how to appraise
theories to the problem of how to appraise series of theories. Not an isolated
theory, but only a series of theories can be said to be scientific or unscient-
ific: to apply the term ‘scientific’ to one single theory is a category mistake.”

The time-honoured empirical criterion for a satisfactory theory was
agreement with the observed facts. Our empirical criterion for a series of
theories is that it should produce new facts. The idea of growth and the
concept of empirical character are soldered into one.

This revised form of methodological falsificationism has many new
features. First, it denies that ‘in the case of a scientific theory, our decision
depends upon the results of experiments. If these confirm the theory, we
may accept it until we find a better one. If they contradict the theory, we
reject it.’ It denies that ‘what ultimately decides the fate of a theory is the
result of a test, i.e. an agreement about basic statements’. Contrary to
naive falsificationism, no experiment, experimental report, observation state-
ment or well-corroborated low-level falsifying hypothesis alone can lead to
falsification.® There is no falsification before the emergence of a better theory.®

1 Indeed, in the original manuscript of my [1968a] I wrote: ‘A theory without excess
corroboration has no excess explanatory power; therefore, according to Popper, it does not
represent growth and therefore it is not “scientific” ; therefore, we should say, it has no explana-
tory power’ (p. 386). I cut out the italicized half of the sentence under pressure from my
colleagues who thought it sounded too eccentric. I regret it now.

2 Popper’s conflation of ‘theories’ and ‘series of theories’ prevented him from getting
the basic ideas of sophisticated falsificationism across more successfully, His ambiguous
usage led to such confusing formulations as ‘Marxism [as the core of a series of theories
or of a “research programme’”’] is irrefutable’ and, at the same time, ‘Marxism [as a
particular conjunction of this core and some specified auxiliary hypotheses, initial con-
ditions and a ceteris paribus clause] has been refuted.’ (Cf. Popper [1963].)

Of course, there is nothing wrong in saying that an isolated, single theory is ‘scientific’
if it represents an advance on its predecessor, as long as one clearly realizes that in this
formulation we appraise the theory as the outcome of—and in the context of—a certain
historical development.

* Popper [1945], vol. II, p. 233. Popper’s more sophisticated attitude surfaces in the
remark that ‘concrete and practical consequences can be more directly tested by experiment’
(ibid. my italics). “ Popper [1934], section 30.

5 For the pragmatic character of methodological ‘falsification’, cf. above, p. 109, footnote 2.

*“In most cases we have, before falsifying a hypothesis, another one up our sleeves’
(Popper [19592], p. 87, footnote *1). But, as our argument shows, we must have one. Or,

as Feyerabend put it: “The best criticism is provided by those theories which can replace
the rivals they have removed’ ([1965], p. 227). He notes that in some cases ‘alternatives

120 IMRE LAKATOS

But then the distinctively negative character of naive falsificationism
vanishes; criticism becomes more difficult, and also positive, constructive.
But, of course, if falsification depends on the emergence of better theories,
on the invention of theories which anticipate new facts, then falsification is
not simply a relation between a theory and the empirical basis, but a
multiple relation between competing theories, the original ‘empirical
basis’, and the empirical growth resulting from the competition. Falsi-
fication can thus be said to have a ‘historical character’.1 Moreover, some of
the theories which bring about falsification are frequently proposed after
the ‘counterevidence’. This may sound paradoxical for people indoc-
trinated with naive falsificationism. Indeed, this epistemological theory of
the relation between theory and experiment differs sharply from the
epistemological theory of naive falsificationism. The very term ‘counter-
evidence’ has to be abandoned in the sense that no experimental result
must be interpreted directly as ‘counterevidence’. If we still want to retain
this time-honoured term, we have to redefine it like this: ‘counterevidence
to T,’ is a corroborating instance to T, which is either inconsistent with or
independent of 7, (with the proviso that T, is a theory which satisfactorily
explains the empirical success of 7,). This shows that ‘crucial counter-
evidence’—or ‘crucial experiments’—can be recognized as such among the
scores of anomalies only with hindsight, in the light of some superseding
theory.”

Thus the crucial element in falsification is whether the new theory offers
any novel, excess information compared with its predecessor and whether
some of this excess information is corroborated. Justificationists valued
‘confirming’ instances of a theory; naive falsificationists stressed ‘refuting’
instances; for the methodological falsificationists it is the—rather rare—
corroborating instances of the excess information which are the crucial
ones; these receive all the attention. We are no longer interested in the

will be quite indispensable for the purpose of refutation’ (ibid. p. 254). But according
to our argument refutation without an alternative shows nothing but the poverty of our imagina-
tion in providing a rescue hypothesis. Also cf. below, p. 121, footnote 4.

1Cf. my [1968a], pp. 387 ff.

2In the distorting mirror of naive falsificationism, new theories which replace old
refuted ones, are themselves born unrefuted. Therefore they do not believe that there is
a relevant difference between anomalies and crucial counterevidence. For them, anomaly
is a dishonest euphemism for counterevidence. But in actual history new theories are
born refuted: they inherit many anomalies of the old theory. Moreover, frequently it is
only the new theory which dramatically predicts that fact which will function as crucial
counterevidence against its predecessor, while the ‘old’. anomalies may well stay on as
‘new’ anomalies.

All this will be still clearer when we introduce the idea of ‘research programme’:
cf. below, pp. 135 and 176 ff.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 1I12I

thousands of trivial verifying instances nor in the hundreds of readily
available anomalies: the few crucial excess-verifying instances are decisive.
This consideration rehabilitates—and reinterprets—the old proverb:
Exemplum docet, exempla obscurant.

‘Falsification’ in the sense of naive falsificationism (corroborated counter-
evidence) is not a sufficient condition for eliminating a specific theory: in
spite of hundreds of known anomalies we do not regard it as falsified (that
is, eliminated) until we have a better one.? Nor is ‘falsification’ in the naive
sense necessary for falsification in the sophisticated sense: a progressive
problemshift does not have to be interspersed with ‘refutations’. Science
can grow without any ‘refutations’ leading the way. Naive falsificationists
suggest a linear growth of science, in the sense that theories are followed by
powerful refutations which eliminate them; these refutations in turn are
followed by new theories.’ It is perfectly possible that theories be put
forward ‘progressively’ in such a rapid succession that the ‘refutation’ of
the n-th appears only as the corroboration of the n+-1-th. The problem
fever of science is raised by proliferation of rival theories rather than
counterexamples or anomalies.

This shows that the slogan of proliferation of theories is much more
important for sophisticated than for naive falsificationism. For the naive
falsificationist science grows through repeated experimental overthrow of
theories; new rival theories proposed before such ‘overthrows’ may speed
up growth but are not absolutely necessary‘; constant proliferation of
theories is optional but not mandatory. For the sophisticated falsificationist

1 Sophisticated falsificationism adumbrates a new theory of learning; cf. below, p. 123.

2 It is clear that the theory T’ may have excess corroborated empirical content over another
theory T even if both T and T” are refuted. Empirical content has nothing to do with
truth or falsity. Corroborated contents can also be compared irrespective of the refuted
content, Thus we may see the rationality of the elimination of Newton’s theory in favour
of Einstein’s, even though Einstein’s theory may be said to have been born—like Newton’s
—‘refuted’, We have only to remember that ‘qualitative confirmation’ is a euphemism for
‘quantitative disconfirmation’. (Cf. my [1968a], pp. 384-6.)

3 Cf, Popper [1934], section 85, p. 279 of the 1959 English translation,

* It is true that a certain type of proliferation of rival theories is allowed to play an
accidental heuristic role in falsification. In many cases falsification heuristically ‘depends
on [the condition] that sufficiently many and sufficiently different theories are offered’
(Popper [1940]). For instance, we may have a theory T which is apparently unrefuted.
But it may happen that a new theory T’, inconsistent with T, is proposed which equally
fits the available facts: the differences are smaller than the range of observational error.
In such cases the inconsistency prods us into improving our ‘experimental techniques’,
and thus refining the ‘empirical basis’ so that either T or T’ (or, incidentally, both) can
be falsified : “We need [a] new theory in order to find out where the old theory was deficient’
(Popper [1963], p. 246). But the role of this proliferation is accidental in the sense that,
once the empirical basis is refined, the fight is between this refined empirical basis and
the theory T under test; the rival theory T’ acted only as a catalyst. (Also cf. above, p. 119,
footnote 6.)

122 IMRE LAKATOS

proliferation of theories cannot wait until the accepted theories are ‘refuted’
(or until their protagonists get into a Kuhnian crisis of confidence).1 While
naive falsificationism stresses ‘the urgency of replacing a falsified hypo-
thesis by a better one’,? sophisticated falsificationism stresses the urgency
of replacing any hypothesis by a better one. Falsification cannot ‘compel
the theorist to search for a better theory’,? simply because falsification
cannot precede the better theory.

The problem-shift from naive to sophisticated falsificationism involves a
semantic difficulty. For the naive falsificationist a ‘refutation’ is an experi-
mental result which, by force of his decisions, is made to conflict with the
theory under test. But according to sophisticated falsificationism one must
not take such decisions before the alleged ‘refuting instance’ has become
the confirming instance of a new, better theory. Therefore whenever we
see terms like ‘refutation’, ‘falsification’, ‘counterexample’, we have to
check in each case whether these terms are being applied in virtue of
decisions by the naive or by the sophisticated falsificationist.4

Sophisticated methodological falsificationism offers new standards for
intellectual honesty. Justificationist honesty demanded the acceptance of
only what was proven and the rejection of everything unproven. Neojusti-
ficationist honesty demanded the specification of the probability of any
hypothesis in the light of the available empirical evidence. The honesty of
naive falsificationism demanded the testing of the falsifiable and the rejec-
tion of the unfalsifiable and the falsified. Finally, the honesty of sophis-
ticated falsificationism demanded that one should try to look at things from
different points of view, to put forward new theories which anticipate
novel facts, and to reject theories which have been superseded by more
powerful ones.

Sophisticated methodological falsificationism blends several different
traditions. From the empiricists it has inherited the determination to learn
primarily from experience. From the Kantians it has taken the activist
approach to the theory of knowledge. From the conventionalists it has
learned the importance of decisions in methodology.

1 Also cf. Feyerabend [1965], pp. 254-5.

2 Popper [1959], p. 87, footnote *1.

3 Popper [1934], section 30.

4Cf. also above, p. 109, footnote 2. [Added in press:] Possibly it would be better in
future to abandon these terms altogether, just as we have abandoned terms like ‘inductive
(or experimental) proof’. Then we may call (naive) ‘refutations’ anomalies, and (sophisti-
catedly) ‘falsified’ theories ‘superseded’ ones. Our ‘ordinary’ language is impregnated
not only by ‘inductivist’ but also by falsificationist dogmatism. A reform is overdue.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 123

I should like to emphasize here a further distinctive feature of sophis-
ticated methodological empiricism: the crucial role of excess corrobora-
tion. For the inductivist, learning about a new theory is learning how much
confirming evidence supports it; about refuted theories one learns nothing
(learning, after all, is to build up proven or probable knowledge). For the
dogmatic falsificationist, learning about a theory is learning whether it is
refuted or not; about confirmed theories one learns nothing (one cannot
prove or probabilify anything), about refuted theories one learns that they
are disproved.1 For the sophisticated falsificationist, learning about a
theory is primarily learning which new facts it anticipated: indeed, for the
sort of Popperian empiricism I advocate, the only relevant evidence is the
evidence anticipated by a theory, and empiricalness (or scientific character)
and theoretical progress are inseparably connected.”

This idea is not entirely new. Leibnitz, for instance, in his famous letter
to Conring in 1678, wrote: ‘It is the greatest commendation of an hypo-
thesis (next to [proven] truth) if by its help predictions can be made even
about phenomena or experiments not tried.’* Leibnitz’s view was widely
accepted by scientists. But since all appraisal of a scientific theory was
before Popper appraisal of its degree of justification, this position was
regarded by some logicians as untenable. Mill, for instance, complains in
1843 in horror that ‘it seems to be thought that an hypothesis . . is entitled
to a more favourable reception, if besides accounting for all the facts
previously known, it has led to the anticipation and prediction of others
which experience afterwards verified’. Mill had a point: this appraisal was
in conflict both with justificationism and with probabilism: why should an
event prove more, if it was anticipated by the theory than if it was known
already before? As long as proof was the only criterion of the scientific
character of a theory, Leibnitz’s criterion could only be regarded as
irrelevant. Also, the probability of a theory given evidence cannot possibly
be influenced, as Keynes pointed out, by when the evidence was produced:
the probability of a theory given evidence can depend only on the theory

1 For a defence of this theory of ‘learning from experience’, cf. Agassi [1969].

2 These remarks show that ‘learning from experience’ is a normative idea; therefore all
purely ‘empirical’ learning theories miss the heart of the problem.

3 Cf. Leibnitz [1678]. The expression in brackets shows that Leibnitz regarded this
criterion as second best and thought that the best theories are those which are proved.
Thus Leibnitz’s position—like Whewell’s—is a far cry from fully fledged sophisticated
falsificationism.

* Mill [1843], vol. m1, p. 23.

§ This was J. S. Mill’s argument (#bid.). He directed it against Whewell, who thought
that ‘consilience of inductions’ or successful prediction of improbable events verifies (that
is, proves) a theory. (Whewell [1858], pp. 95-6.) No doubt, the basic contradiction both in
Whewell’s and in Duhem's philosophy of science is their conflation of heuristic power and
proven truth, Popper separated the two.

124 IMRE LAKATOS

and the evidence,’ and not upon whether the evidence was produced
before or after the theory.

In spite of this convincing justificationist criticism, the criterion sur-
vived among some of the best scientists, since it formulated their strong
dislike of merely ad hoc explanations, which ‘though [they] truly express the
facts [they set out to explain, are] not born out by any other phenomena’.”

But it was only Popper who recognized that the prima facie inconsistency
between the few odd, casual remarks against ad hoc hypotheses on the one
hand and the huge edifice of justificationist philosophy of knowledge must
be solved by demolishing justificationism and by introducing new, non-
justificationist criteria for appraising scientific theories based on anti-
adhocness.

Let us look at a few examples. Einstein’s theory is not better than
Newton’s because Newton’s theory was ‘refuted’ but Einstein’s was not:
there are many known ‘anomalies’ to Einsteinian theory. Einstein’s theory
is better than—that is, represents progress compared with—Newton’s
theory anno 1916 (that is, Newton’s laws of dynamics, law of gravitation,
the known set of initial conditions; ‘minus’ the list of known anomalies
such as Mercury’s perihelion) because it explained everything that Newton’s
theory had successfully explained, and it explained also to some extent some
known anomalies and, in addition, forbade events like transmission of light
along straight lines near large masses about which Newton’s theory had
said nothing but which had been permitted by other well-corroborated
scientific theories of the day; moreover, at least some of the unexpected
excess Einsteinian content was in fact corroborated (for instance, by the
eclipse experiments).

On the other hand, according to these sophisticated standards, Galileo’s
theory that the natural motion of terrestrial objects was circular, intro-
duced no improvement since it did not forbid anything that had not been
forbidden by the relevant theories he intended to improve upon (that is, by
Aristotelian physics and by Copernican celestial kinematics). This theory
was therefore ad hoc and therefore—from the heuristic point of view—
valueless.?

A beautiful example of a theory which satisfied only the first part of
Popper’s criterion of progress (excess content) but not the second part
(corroborated excess content) was given by Popper himself: the Bohr-

1 Keynes [1921], p. 305. But cf. my [1968a], p. 394.

2 This is Whewell’s critical comment on an ad hoc auxiliary hypothesis in Newton’s
theory of light (Whewell [1857], vol. u, p. 317.)

3 In the terminology of my [1968a], this theory was ‘ad hoc,’ (cf. my [1968a], p. 389,

footnote 1); the example was originally suggested to me by Paul Feyerabend as a paradigm
of a valuable ad hoc theory. But cf. below, p. 142, especially footnote 3.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 125

Kramers-Slater theory of 1924. This theory was refuted in all its new
predictions.+

Let us finally consider how much conventionalism remains in sophis-
ticated falsificationism. Certainly Jess than in naive falsificationism. We
need fewer methodological decisions. The ‘fourth-type decision’ which was
essential for the naive version? has become completely redundant. To
show this we only have to realize that if a scientific theory, consisting of
some ‘laws of nature’, initial conditions, auxiliary theories (but without a
ceteris paribus clause) conflicts with some factual propositions we do not
have to decide which—explicit or ‘hidden’—part to replace. We may try to
replace any part and only when we have hit on an explanation of the
anomaly with the help of some content-increasing change (or auxiliary
hypothesis), and nature corroborates it, do we move on to eliminate the
‘refuted’ complex. Thus sophisticated falsification is a slower but possibly
safer process than naive falsification.

Let us take an example. Let us assume that the course of a planet
differs from the one predicted. Some conclude that this refutes the dyn-
amics and gravitational theory applied: the initial conditions and the
ceteris paribus clause have been ingeniously corroborated. Others conclude
that this refutes the initial conditions used in the calculations: dynamics
and gravitational theory have been superbly corroborated in the last two
hundred years and all suggestions concerning further factors in play failed.
Yet others conclude that this refutes the underlying assumption that there
were no other factors in play except for those which were taken into
account: these people may possibly be motivated by the metaphysical
principle that any explanation is only approximative because of the infinite
complexity of the factors involved in determining any single event. Should
we praise the first type as ‘critical’, scold the second type as ‘hack’, and
condemn the third as ‘apologetic’? No. We do not need to draw any con-
clusions about such ‘refutation’. We never reject a specific theory simply
by fiat. If we have an inconsistency like the one mentioned, we do not
have to decide which ingredients of the theory we regard as problematic
and which ones as unproblematic: we regard all ingredients as problem-
atic in the light of the conflicting accepted basic statement and try to
replace all of them. If we succeed in replacing some ingredient in a ‘pro-
gressive’ way (that is, the replacement has more corroborated empirical
content than the original), we call it ‘falsified’.

We do not need the fifth type decision of the naive falsificationist either.

1 In the terminology of my [1968a], this theory was not ‘ad hoc,’, but it was ‘ad hoc,’
(cf. my [1968a], p. 389, footnote 1). For a simple but artificial illustration, see ibid. p. 387,
footnote 2. (For ad hoes, cf. below, p. 175, footnote 3.) 2 Cf. above, p. t10.

126 IMRE LAKATOS

In order to show this let us have a new look at the problem of the appraisal
of (syntactically) metaphysical theories—and the problem of their retention
and elimination. The ‘sophisticated’ solution is obvious. We retain a
syntactically metaphysical theory as long as the problematic instances can
be explained by content-increasing changes in the auxiliary hypotheses
appended to it.1 Let us take, for instance, Cartesian metaphysics C: ‘in all
natural processes there is a clockwork mechanism regulated by (a prior?)
animating principles.’ This is syntactically irrefutable: it can clash with
no—spatiotemporally singular—‘basic statement’. It may, of course, clash
with a refutable theory like N: ‘gravitation is a force equal to fm, m,/r*
which acts at a distance’. But N will only clash with C if ‘action at a distance’
is interpreted literally and possibly, in addition, as representing an ultimate
truth, irreducible to any still deeper cause. (Popper would call this an
‘essentialist’ interpretation.) Alternatively we can regard ‘action at a dis-
tance’ as a mediate cause. Then we interpret ‘action at a distance’ figurativ-
ely, and regard it as a shorthand for some hidden mechanism of action
by contact. (We may call this a ‘nominalist’ interpretation.) In this case
we can attempt to explain N by C—Newton himself and several French
physicists of the eighteenth century tried to do so. If an auxiliary theory
which performs this explanation (or, if you wish, ‘reduction’) produces
novel facts (that is, it is ‘independently testable’), Cartesian metaphysics
should be regarded as good, scientific, empirical metaphysics, generating
a progressive problemshift. A progressive (syntactically) metaphysical
theory produces a sustained progressive shift in its protective belt of
auxiliary theories. If the reduction of the theory to the ‘metaphysical’ frame-
work does not produce new empirical content, let alone novel facts, then
the reduction represents a degenerating problemshift, it is a mere linguistic
exercise. The Cartesian efforts to bolster up their ‘metaphysics’ in order to
explain Newtonian gravitation is an outstanding example of such a merely
linguistic reduction.”

Thus we do not eliminate a (syntactically) metaphysical theory if it
clashes with a well-corroborated scientific theory, as naive falsificationism
suggests. We eliminate it if it produces a degenerating shift in the long
run and there is a better, rival, metaphysics to replace it. The methodology

1 We can formulate this condition with striking clarity only in terms of the methodology
of research programmes to be explained in §3: we retain a syntactically metaphysical theory
as the ‘hard core’ of a research programme as long as its associated positive heuristic produces a
progressive problemshift in the ‘protective belt’ of auxiliary hypotheses. Cf. below, pp. 136-7.

2This phenomenon was described in a beautiful paper by Whewell [1851]; but he
could not explain it methodologically. Instead of recognizing the victory of the progressive
Newtonian programme over the degenerating Cartesian programme, he thought this was
the victory of proven truth over falsity. For details cf. my [1970]: for a general discussion
of the demarcation between progressive and degenerating reduction cf. Popper [1969].

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 127

of a research programme with a ‘metaphysical’ core does not differ from
the methodology of one with a ‘refutable’ core except for the logical level
of the inconsistencies which are the driving force of the programme.

(It has to be stressed, however, that the very choice of the logical form
in which to articulate a theory depends to a large extent on our method-
ological decision. For instance, instead of formulating Cartesian meta-
physics as an ‘all-some’ statement, we can formulate it as an ‘all-statement’:
‘all natural processes are clockworks’. A ‘basic statement’ contradicting
this would be: ‘a is a natural process and it is not clockwork’. The question
is whether according to the ‘experimental techniques’, or rather, to the
interpretative theories of the day, ‘x is not a clockwork’ can be ‘established’
or not. Thus the rational choice of the logical form of a theory depends on
the state of our knowledge; for instance, a metaphysical ‘all-some’ state-
ment of today may become, with the change in the level of observational
theories, a scientific ‘all-statement’ tomorrow. I have already argued that
only series of theories and not theories should be classified as scientific or
non-scientific; now I have indicated that even the logical form of a theory
can only be rationally chosen on the basis of a critical appraisal of the state
of the research programme in which it is embedded.)

The first, second, and third type decisions of naive falsificationism?
however cannot be avoided, but as we shall show, the conventional
element in the second decision—and also in the third—-can be slightly
reduced. We cannot avoid the decision which sort of propositions should
be the ‘observational’ ones and which the ‘theoretical’ ones. We cannot
avoid either the decision about the truth-value of some ‘observational
propositions’. These decisions are vital for the decision whether a problem-
shift is empirically progressive or degenerating.* But the sophisticated
falsificationist may at least mitigate the arbitrariness of this second decision
by allowing for an appeal procedure.

Naive falsificationists do not lay down any such appeal procedure. ‘They
accept a basic statement if it is backed up by a well-corroborated falsifying
hypothesis,* and let it overrule the theory under test—even though they
are well aware of the risk.5 But there is no reason why we should not regard
a falsifying hypothesis—and the basic statement it supports—as being just
as problematic as a falsified hypothesis. Now how exactly can we expose
the problematicality of a basic statement? On what grounds can the pro-
tagonists of the ‘falsified’ theory appeal and win?

Some people may say that we might go on testing the basic statement (or

1 Cf. above, p. 126, footnote 1, 2 Cf. above, pp. 106 and 109.
3 Cf. above, p. 118. * Popper [1934], section 22.
5 Cf. e.g. Popper [1959a], p. 107, footnote *2. Also cf. above, pp. 112-14.

128 IMRE LAKATOS

the falsifying hypothesis) ‘by their deductive consequences’ until agree-
ment is finally reached. In this testing we deduce—in the same deductive
model—further consequences from the basic statement either with the
help of the theory under test or some other theory which we regard as
unproblematic. Although this procedure ‘has no natural end’, we always
come to a point when there is no further disagreement.

But when the theoretician appeals against the verdict of the experi-
mentalist, the appeal court does not normally cross-question the basic
statement directly but rather questions the interpretative theory in the light
of which its truth-value had been established.

One typical example of a series of successful appeals is the Proutians’
fight against unfavourable experimental evidence from 1815 to 1911. For
decades Prout’s theory T (‘that all atoms are compounds of hydrogen
atoms and thus ‘atomic weights” of all chemical elements must be ex-
pressible as whole numbers’) and falsifying ‘observational’ hypotheses,
like Stas’s ‘refutation’ R (‘the atomic weight of chlorine is 35-5’) con-
fronted each other. As we know, in the end T prevailed over R.?

The first stage of any serious criticism of a scientific theory is to re-
construct, improve, its logical deductive articulation. Let us do this in the
case of Prout’s theory vis d vis Stas’s refutation. First of all, we have to
realize that in the formulation we just quoted, T and R were not incon-
sistent. (Physicists rarely articulate their theories sufficiently to be pinned
down and caught by the critic.) In order to show them up as inconsistent
we have to put them in the following form. T: ‘the atomic weight of all pure
(homogeneous) chemical elements are multiples of the atomic weight of
hydrogen’, and R: ‘chlorine is a pure (homogeneous) chemical element and
its atomic weight is 35-5’. The last statement is in the form of a falsifying
hypothesis which, if well corroborated, would allow us to use basic state-
ments of the form B: ‘Chlorine X is a pure (homogeneous) chemical
element and its atomic weight is 35-5’—-where X is the proper name of a
‘piece’ of chlorine determined, say, by its space-time co-ordinates.

But how well-corroborated is R? The first component of it says that R,:
‘Chlorine X is a pure chemical element.’ This was the verdict of the
experimental chemist after a rigorous application of the ‘experimental
techniques’ of the day.

Let us have a closer look at the fine-structure of R,. In fact R, stands for
a conjunction of two longer statements 7, and 7,. The first statement,

1 This is argued in Popper [1934], section 29.

2 Agassi claims that this example shows that we may ‘stick to the hypothesis in the
face of known facts in the hope that the facts will adjust themselves to theory rather than
the other way round’ ({1966], p. 18). But Aow can facts ‘adjust themselves’? Under which
particular conditions should the theory win? Agassi gives no answer.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 129

T,, could be this: ‘If seventeen chemical purifying procedures ,, py. . - Py
are applied to a gas, what remains will be pure chlorine.’ T, is then: ‘X
was subjected to the seventeen procedures ~,, po... 7. The careful
‘experimenter’ carefully applied all seventeen procedures: T, is to be
accepted. But the conclusion that therefore what remained must be pure
chlorine is a ‘hard fact’ only in virtue of T,. The experimentalist, while
testing T, applied T,. He interpreted what he saw in the light of 7,: the
result was R,. Yet in the monotheoretical model of the explanatory theory
under test this interpretative theory does not appear at all.

But what if 7, the interpretative theory, is false? Why not ‘apply’ T
rather than T, and claim that atomic weights must be whole numbers? Then
this will be a ‘hard fact’ in the light of 7, and 7, will be overthrown.
Perhaps additional new purifying procedures must be invented and applied.

The problem is then not when we should stick to a ‘theory’ in the face of
‘known facts’ and when the other way round. The problem is not what to do
when ‘theories’ clash with ‘facts’. Such a ‘clash’ is only suggested by the
‘monotheoretical deductive model’, Whether a proposition is a ‘fact’ or a
‘theory’ in the context of a test-situation depends on our methodological
decision. ‘Empirical basis of a theory’ is a mono-theoretical notion, it is
relative to some mono-theoretical deductive structure. We may use it as first
approximation; but in case of ‘appeal’ by the theoretician, we must use a
pluralistic model. In the pluralistic model the clash is not ‘between theories
and facts’ but between two high-level theories: between an interpretative
theory to provide the facts and an explanatory theory to explain them ; and the
interpretative theory may be on quite as high a level as the explanatory
theory. The clash is then not any more between a logically higher-level
theory and a lower-level falsifying hypothesis. The problem should not be
put in terms of whether a ‘refutation’ is real or not. The problem is how to
repair an inconsistency between the ‘explanatory theory’ under test and the
—explicit or hidden—‘interpretative’ theories; or, if you wish, the problem
is which theory to consider as the interpretative one which provides the ‘hard’
facts and which the explanatory one which ‘tentatively’ explains them. In a
mono-theoretical model we regard the higher-level theory as an explan-
atory theory to be judged by the ‘facts’ delivered from outside (by the author-
itative experimentalist): in the case of a clash we reject the explanation.!
In a pluralistic model we may decide, alternatively, to regard the higher-

1 The decision to use some monotheoretical model is clearly vital for the naive falsifica-
tionist to enable him to reject a theory on the sole ground of experimental evidence. It is
in line with the necessity for him to divide sharply, at least in a test-situation, the body of
science into two: the problematic and the unproblematic. (Cf. above p.107.) It is only the

theory he decides to regard as problematic which he articulates in his deductive model of
criticism.

130 IMRE LAKATOS

level theory as an interpretative theory to judge the ‘facts’ delivered from
outside: in case of a clash we may reject the ‘facts’ as ‘monsters’. In a
pluralistic model of testing, several theories—more or less deductively
organized—are soldered together.

This argument alone would be enough to show the correctness of the
conclusion, which we drew from a different earlier argument, that experi-
ments do not simply overthrow theories, that no theory forbids a state of
affairs specifiable in advance.! It is not that we propose a theory and Nature
may shout NO; rather, we propose a maze of theories, and Nature may
shout INCONSISTENT.?

The problem is then shifted from the old problem of replacing a theory
refuted by ‘facts’ to the new problem of how to resolve inconsistencies
between closely associated theories. Which of the mutually inconsistent
theories should be eliminated? The sophisticated falsificationist can answer
that question easily: one had to try to replace first one, then the other, then
possibly both, and opt for that new set-up which provides the biggest
increase in corroborated content, which provides the most progressive
problemshift.$

Thus we have established an appeal procedure in case the theoretician
wishes to question the negative verdict of the experimentalist. The theore-
tician may demand that the experimentalist specify his ‘interpretative
theory’,4 and he may then replace it—to the experimentalist’s annoyance—
by a better one in the light of which his originally ‘refuted’ theory may
receive positive appraisal.®

1 Cf. above, p. 100.

? Let me here answer a possible objection: ‘Surely we do not need Nature to tell us
that a set of theories is inconsistent. Inconsistency—unlike falsehood—can be ascertained
without Nature’s help’. But Nature’s actual ‘NO’ in a monotheoretical methodology takes
the form of a fortified ‘potential falsifier’, that is a sentence which, in this way of speech,
we claim Nature had uttered and which is the negation of our theory. Nature’s actual
‘INCONSISTENCY’ in a pluralistic methodology takes the form of a ‘factual’ statement
couched in the light of one of the theories involved, which we claim Nature had uttered
and which, if added to our proposed theories, yields an inconsistent system,

3 For instance, in our earlier example (cf. above, p. 107 ff.) some may try to replace the
gravitational theory with a new one and others may try to replace the radio-optics by a new
one: we choose the way which offers the more spectacular growth, the more progressive
problemshift.

4 Criticism does not assume a fully articulated deductive structure: it creates it. (Inci-
dentally, this is the main message of my [1963-4].)

5 A classical example of this pattern is Newton’s relation to Flamsteed, the first Astro-
nomer Royal. For instance, Newton visited Flamsteed on 1 September 1694, when working
full time on his lunar theory; told him to reinterpret some of his data since they contra-
dicted his own theory; and he explained to him exactly how to do it. Flamsteed obeyed
Newton and wrote to him on 7 October: ‘Since you went home, I examined the observa-

tions I employed for determining the greatest equations of the earth’s orbit, and consider-
ing the moon’s places at the times...’ I find that (i, as you intimate, the earth inclines

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 131

But even this appeal procedure cannot do more than postpone the con-
ventional decision. For the verdict of the appeal court is not infallible
either. When we decide whether it is the replacement of the ‘interpretative’
or of the ‘explanatory’ theory that produces novel facts, we again must take
a decision about the acceptance or rejection of basic statements. But then
we have only postponed—and possibly improved—the decision, not avoided
it.1 The difficulties concerning the empirical basis which confronted ‘naive’
falsificationism cannot be avoided by ‘sophisticated’ falsificationism either.
Even if we regard a theory as ‘factual’, that is, if our slow-moving and
limited imagination cannot offer an alternative to it (as Feyerabend used to
put it), we have to make, at least occasionally and temporarily, decisions
about its truth-value. Even then, experience still remains, in an important
sense, the ‘impartial arbiter’® of scientific controversy. We cannot get rid of
the problem of the ‘empirical basis’, if we want to learn from experience?:
but we can make our learning less dogmatic—but also less fast and less
dramatic. By regarding some observational theories as problematic we
may make our methodology more flexible: but we cannot articulate and
include all ‘background knowledge’ (or ‘background ignorance’?) into our
critical deductive model. This process is bound to be piecemeal and some
conventional line must be drawn at any given time.

There is one objection even to the sophisticated version of methodologi-
cal falsificationism which cannot be answered without some concession to
Duhemian ‘simplicism’. The objection is the so-called ‘tacking paradox’.
According to our definitions, adding to a theory completely disconnected
low-level hypotheses may constitute a ‘progressive shift’. It is difficult to
eliminate such makeshift shifts without demanding that ‘the additional
assertions must be connected with the contradicting assertion more inti-
mately than by mere conjunction’.* This, of course, is a sort of simplicity

on that side the moon then is) you may abate abt 20” from it...” Thus Newton constantly
criticized and corrected Flamsteed’s observational theories. Newton taught Flamsteed,
for instance, a better theory of the refractive power of the atmosphere; Flamsteed accepted
this and corrected his original ‘data’. One can understand the constant humiliation and
slowly increasing fury of this great observer, having his data criticized and improved by
a man who, on his own confession, made no observations himself: it was this feeling—
I suspect—which led finally to,a vicious personal controversy.

1 The same applies to the third type of decision. If we reject a stochastic hypothesis only
for one which, in our sense, supersedes it, the exact form of the ‘rejection rules’ becomes
less important.

2 Popper [1945], vol. 11, chapter 23, p. 218.

3 Agassi is then wrong in his thesis that ‘observation reports may be accepted as false
and hence the problem of the empirical basis is thereby disposed of’ (Agassi [1966], p. 20).

4 Feyerabend [1965], p. 226.

132 IMRE LAKATOS

requirement which would assure the continuity in the series of theories
which can be said to constitute one problemshift.

This leads us to further problems. For one of the crucial features of
sophisticated falsificationism is that it replaces the concept of theory as the
basic concept of the logic of discovery by the concept of series of theories.
It is a succession of theories and not one given theory which is appraised as
scientific or pseudo-scientific. But the members of such series of theories are
usually connected by a remarkable continuity which welds them into
research programmes. This continuity—reminiscent of Kuhnian ‘normal
science’—plays a vital role in the history of science; the main problems of
the logic of discovery cannot be satisfactorily discussed except in the frame-
work of a methodology of research programmes.

3. A METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES

I have discussed the problem of objective appraisal of scientific growth in
terms of progressive and degenerating problemshifts in series of scientific
theories. The most important such series in the growth of science are
characterized by a certain continuity which connects their members. This
continuity evolves from a genuine research programme adumbrated at the
start.1 The programme consists of methodological rules: some tell us what
paths of research to avoid (negative heuristic), and others what paths to
pursue (positive heuristic),

Even science as a whole can be regarded as a huge research programme
with Popper’s supreme heuristic rule: ‘devise conjectures which have more
empirical content than their predecessors.’ Such methodological rules may
be formulated, as Popper pointed out, as metaphysical principles.? For
instance, the universal anti-conventionalist rule against exception-barring
may be stated as the metaphysical principle: ‘Nature does not allow excep-
tions’. This is why Watkins called such rules ‘influential metaphysics’ .®

But what I have primarily in mind is not science as a whole, but rather
particular research programmes, such as the one known as ‘Cartesian
metaphysics’. Cartesian metaphysics, that is, the mechanistic theory of the

1 One may point out that the negative and positive heuristic gives a rough (implicit)
definition of the ‘conceptual framework’ (and consequently of the language). The recogni-
tion that the history of science is the history of research programmes rather than of
theories may therefore be seen as a partial vindication of the view that the history of
science is the history of conceptual frameworks or of scientific languages.

2 Popper [1934], sections 11 and 70. I use ‘metaphysical’ as a technical term of naive
falsificationism: a contingent proposition is ‘metaphysical’ if it has no ‘potential falsifiers’ .

3 Watkins [1958]. Watkins cautions that ‘the logical gap between statements and pre-
scriptions in the metaphysical-methodological field is illustrated by the fact that a person

may reject a [metaphysical] doctrine in its fact-stating form while subscribing to the
prescriptive version of it’ ({bid. pp. 356-7).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 133

universe—according to which the universe is a huge clockwork (and system
of vortices) with push as the only cause of motion—functioned as a power-
ful heuristic principle. It discouraged work on scientific theories—like [the
‘essentialist’ version of] Newton’s theory of action at a distance—which
were inconsistent with it (negative heuristic). On the other hand, it encour-
aged work on auxiliary hypotheses which might have saved it from apparent
counterevidence—like Keplerian ellipses (positive heuristic).

(a) Negative heuristic: the ‘hard core’ of the programme.

All scientific research programmes may be characterized by their ‘hard
core’, The negative heuristic of the programme forbids us to direct the
modus tollens at this ‘hard core’. Instead, we must use our ingenuity to artic-
ulate or even invent ‘auxiliary hypotheses’, which form a protective belt
around this core, and we must redirect the modus tollens to these. It is this
protective belt of auxiliary hypotheses which has to bear the brunt of tests
and get adjusted and re-adjusted, or even completely replaced, to defend
the thus-hardened core. A research programme is successful if all this leads
to a progressive problemshift; unsuccessful if it leads to a degenerating
problemshift.

The classical example of a successful research programme is Newton’s
gravitational theory: possibly the most successful research programme ever.
When it was first produced, it was submerged in an ocean of ‘anomalies’
(or, if you wish, ‘counterexamples’”?), and opposed by the observational
theories supporting these anomalies. But Newtonians turned, with brilliant
tenacity and ingenuity, one counter-instance after another into corrobor-
ating instances, primarily by overthrowing the original observational
theories in the light of which this ‘contrary evidence’ was established. In
the process they themselves produced new counter-examples which they
again resolved. They ‘turned each new difficulty into a new victory of their
programme’.®

In Newton’s programme the negative heuristic bids us to divert the
modus tollens from Newton’s three laws of dynamics and his law of gravita-
tion. This ‘core’ is ‘irrefutable’ by the methodological decision of its pro-
tagonists: anomalies must lead to changes only in the ‘protective’ belt of
auxiliary, ‘observational’ hypothesis and initial conditions.‘

I have given a contrived micro-example of a progressive Newtonian

1 Forthis Cartesianresearch programme, cf. Popper [1958] and Watkins [1958], pp. 350-1.

2 For the clarification of the concepts of ‘counterexample’ and ‘anomaly’ cf. above, p. 110,
and especially below, p. 159, footnote 1. 3 Laplace [1796], livre tv, chapter ii.

“The actual hard core of a programme does not actually emerge fully armed like

Athene from the head of Zeus. It develops slowly, by a long, preliminary process of trial
and error. In this paper this process is not discussed.

134 IMRE LAKATOS

problemshift.! If we analyse it, it turns out that each successive link in
this exercise predicts some new fact; each step represents an increase in
empirical content: the example constitutes a consistently progressive theo-
retical shift. Also, each prediction is in the end verified; although on three
subsequent occasions they may have seemed momentarily to be ‘refuted’.?
While ‘theoretical progress’ (in the sense here described) may be verified
immediately,’ ‘empirical progress’ cannot, and in a research programme we
may be frustrated by a long series of ‘refutations’ before ingenious and
lucky content-increasing auxiliary hypotheses turn a chain of defeats—with
hindsight—into a resounding success story, either by revising some false
‘facts’ or by adding novel auxiliary hypotheses. We may then say that we
must require that each step of a research programme be consistently
content-increasing: that each step constitute a consistently progressive
theoretical problemshift. All we need in addition to this is that at least every
now and then the increase in content should be seen to be retrospectively
corroborated: the programme as a whole should also display an zter-
mittently progressive empirical shift. We do not demand that each step
produce immediately an observed new fact. Our term ‘intermittently’ gives
sufficient rational scope for dogmatic adherence to a programme in face of
prima facie ‘refutations’.

The idea of ‘negative heuristic’ of a scientific research programme
rationalizes classical conventionalism to a considerable extent. We may
rationally decide not to allow ‘refutations’ to transmit falsity to the hard
core as long as the corroborated empirical content of the protecting belt
of auxiliary hypotheses increases. But our approach differs from Poincaré’s
justificationist conventionalism in the sense that, unlike Poincaré’s, we
maintain that if and when the programme ceases to anticipate novel facts,
its hard core might have to be abandoned: that is, our hard core, unlike
Poincaré’s, may crumble under certain conditions. In this sense we side
with Duhem who thought that such a possibility must be allowed for*;
but for Duhem the reason for such crumbling is purely aesthetic,5 while
for us it is mainly logical and empirical.

(b) Positive heuristic: the construction of the ‘protective belt’ and the relative
autonomy of theoretical science.

Research programmes, besides their negative heuristic, are also charac-
terized by their positive heuristic.

1 Cf. above, pp. 100-1. For real examples, cf. my [1970].

2 The ‘refutation’ was each time successfully diverted to ‘hidden lemmas’; that is,
to lemmas emerging, as it were, from the ceteris paribus clause.

? But cf. below, pp. 155-7. ‘Cf. above, p. 105. § Ibid,

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 135

Even the most rapidly and consistently progressive research programmes
can digest their ‘counter-evidence’ only piecemeal: anomalies are never
completely exhausted. But it should not be thought that yet unexplained
anomalies—‘puzzles’ as Kuhn might call them—are taken in random
order, and the protective belt built up in an eclectic fashion, without any
preconceived order. The order is usually decided in the theoretician’s
cabinet, independently of the known anomalies. Few theoretical scientists
engaged in a research programme pay undue attention to ‘refutations’.
They have a long-term research policy which anticipates these refutations.
This research policy, or order of research, is set out—in more or less
detail—in the postteve heuristic of the research programme. The negative
heuristic specifies the ‘hard core’ of the programme which is ‘irrefutable’
by the methodological decision of its protagonists; the positive heuristic
consists of a partially articulated set of suggestions or hints on how to
change, develop the ‘refutable variants’ of the research-programme, how
to modify, sophisticate, the ‘refutable’ protective belt.

The positive heuristic of the programme saves the scientist from be-
coming confused by the ocean of anomalies. The positive heuristic sets out
a programme which lists a chain of ever more complicated models simulating
reality: the scientist’s attention is riveted on building his models following
instructions which are laid down in the positive part of his programme. He
ignores the actual counterexamples, the available ‘data’.1 Newton first
worked out his programme for a planetary system with a fixed point-like
sun and one single point-like planet. It was in this model that he derived
his inverse square law for Kepler’s ellipse. But this medel was forbidden by
Newton’s own third law of dynamics, therefore the model had to be replaced
by one in which both sun and planet revolved round their common centre
of gravity. This change was not motivated by any observation (the data did
not suggest an ‘anomaly’ here) but by a theoretical difficulty in developing
the programme, Then he worked out the programme for more planets as
if there were only heliocentric but no interplanetary forces. Then he worked
out the case where the sun and planets were not mass-points but mass-
balls. Again, for this change he did not need the observation of an anomaly;
infinite density was forbidden by an (inarticulated) touchstone theory,
therefore planets had to be extended. This change involved considerable
mathematical difficulties, held up Newton’s work—and delayed the pub-
lication of the Principia by more than a decade. Having solved this ‘puzzle’,

1 If a scientist (or mathematician) has a positive heuristic, he refuses to be drawn into
observation. He will ‘lie down on his couch, shut his eyes and forget about the data’.
(Cf. my [(1963~4], especially pp. 300 ff., where there is a detailed case study of such a
programme.) Occasionally, of course, he will ask Nature a shrewd question: he will then
be encouraged by Nature’s YES, but not discouraged by its NO.

136 IMRE LAKATOS

he started work on spinning balls and their wobbles. Then he admitted
interplanetary forces and started work on perturbations. At this point he
started to look more anxiously at the facts. Many of them were beautifully
explained (qualitatively) by this model, many were not. It was then that he
started to work on bulging planets, rather than round planets, etc.

Newton despised people who, like Hooke, stumbled on a first naive
model but did not have the tenacity and ability to develop it into a research
programme, and who thought that a first version, a mere aside, constituted
a ‘discovery’. He held up publication until his programme had achieved a
remarkable progressive shift.

Most, if not all, Newtonian ‘puzzles’, leading to a series of new variants
superseding each other, were forseeable at the time of Newton’s first naive
model and no doubt Newton and his colleagues did forsee them: Newton
must have been fully aware of the blatant falsity of his first variants.”
Nothing shows the existence of a positive heuristic of aresearch programme
clearer than this fact: this is why one speaks of ‘models’ in research pro-
grammes. A ‘model’ is a set of initial conditions (possibly together with
some of the observational theories) which one knows is bound to be re-
placed during the further development of the programme, and one even
knows, more or less, how. This shows once more how irrelevant ‘refuta-
tions’ of any specific variant are in a research programme: their existence
is fully expected, the positive heuristic is there as the strategy both for
predicting (producing) and digesting them. Indeed, if the positive heuris-
tic is clearly spelt out, the difficulties of the programme are mathematical
rather than empirical.®

One may formulate the ‘positive heuristic’ of a research programme as a
‘metaphysical’ principle. For instance one may formulate Newton’s pro-
gramme like this: ‘the planets are essentially gravitating spinning-tops of
roughly spherical shape’. This idea was never rigidly maintained: the
planets are not just gravitational, they have also, for example, electro-
magnetic characteristics which may influence their motion. Positive heur-

1 Reichenbach, following Cajori, gives a different explanation of what delayed Newton
in the publication of his Principia: ‘To his disappointment he found that the observational
results disagreed with his calculations. Rather than set any theory, however beautiful,
before the facts, Newton put the manuscript of his theory into his drawer. Some twenty
years later, after new measurements of the circumference of the earth had been made by
a French expedition, Newton saw that the figures on which he had based his test were
false and that the improved figures agreed with his theoretical calculation. It was only
after this test that he published his law... The story of Newton is one of the most
striking illustrations of the method of modern science’ (Reichenbach [1951], pp. 101-2).
Feyerabend criticizes Reichenbach’s account (Feyerabend [1965], p. 229), but does not
give an alternative rationale.

2 For a further discussion of Newton’s research programme, cf. my [1970].

3 For this point cf. Truesdell [1960].

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 137

istic is thus in general more flexible than negative heuristic. Moreover, it
occasionally happens that when a research programme gets into a degener-
ating phase, a little revolution or a creative shift in its positive heuristic
may push it forward again. It is better therefore to separate the ‘hard
core’ from the more flexible metaphysical principles expressing the posi-
tive heuristic.

Our considerations show that the positive heuristic forges ahead with
almost complete disregard of ‘refutations’: it may seem that it is the
‘verifications’? rather than the refutations which provide the contact points
with reality. Although one must point out that any ‘verification’ of the
n-+-1-th version of the programme is a refutation of the 7-th version,
we cannot deny that some defeats of the subsequent versions are always
foreseen: it is the ‘verifications’ which keep the programme going, recal-
citrant instances notwithstanding.

We may appraise research programmes, even after their ‘elimination’, for
their heuristic power: how many new facts did they produce, how great was
‘their capacity to explain their refutations in the course of their growth’?

(We may also appraise them for the stimulus they gave to mathematics.
The real difficulties for the theoretical scientist arise rather from the
mathematical difficulties of the programme than from anomalies. The great-
ness of the Newtonian programme comes partly from the development—
by Newtonians—of classical infinitesimal analysis which was a crucial
precondition of its success.)

Thus the methodology of scientific research programmes accounts for
the relative autonomy of theoretical science: a historical fact whose ration-
ality cannot be explained by the earlier falsificationists. Which problems
scientists working in powerful research programmes rationally choose, is
determined by the positive heuristic of the programme rather than by
psychologically worrying (or technologically urgent) anomalies. The
anomalies are listed but shoved aside in the hope that they will turn, in
due course, into corroborations of the programme. Only those scientists
have to rivet their attention on anomalies who are either engaged in trial-
and-error exercises* or who work in a degenerating phase of a research
programme when the positive heuristic ran out of steam. (All this, of

course, must sound repugnant to naive falsificationists who hold that once

1 Soddy’s contribution to Prout’s programme or Pauli’s to Bohr’s (old quantum theory)
programme are typical examples of such creative shifts.

2 A ‘verification’ is a corroboration of excess content in the expanding programme. But,
of course, a ‘verification’ does not verify a programme: it shows only its heuristic power.

3 Cf. my [1963-4], pp. 324-30.. Unfortunately in 1963-4 I had not yet made a clear
terminological distinction between theories and research programmes, and this impaired
my exposition of a research programme in informal, quasi-empirical mathematics. There
are fewer such shortcomings in my [1971]. * Cf. below, p. 175.

138 IMRE LAKATOS

a theory is ‘refuted’ by experiment (by their rule book), it is irrational (and
dishonest) to develop it further: one has to replace the old ‘refuted’ theory
by a new, unrefuted one.)

The dialectic of positive and negative heuristic in a research programme
can best be illuminated by examples. Therefore Iam now going to sketch
a few aspects of two spectacularly successful research programmes: Prout’s
programme? based on the idea that all atoms are compounded of hydrogen
atoms and Bohr’s programme based on the idea that light-emission is due
to electrons jumping from one orbit to another within the atoms.

(In writing a historical case study, one should, I think, adopt the following
procedure: (1) one gives a rational reconstruction; (2) one tries to compare this
rational reconstruction with actual history and to criticize both one’s rational
reconstruction for lack of historicity and the actual history for lack of ration-
ality. Thus any historical study must be preceded by a heuristic study: history
of science without philosophy of science is blind. In this paper it is not my
purpose to go on seriously to the second stage.)

(cr) Prout: a research programme progressing in an ocean of anomalies.
Prout, in an anonymous paper of 1815, claimed that the atomic weights
of all pure chemical elements were whole numbers. He knew very well
that anomalies abounded, but said that these arose because chemical sub-
stances as they ordinarily occurred were impure: that is, the relevant
‘experimental techniques’ of the time were unreliable, or, to put it in
our terms, the contemporary ‘observational’ theories in the light of
which the truth values of the basic statements of his theory were established,
were false.2 The champions of Prout’s theory therefore embarked on a
major venture: to overthrow those theories which supplied the counter-
evidence to their thesis. For this they had to revolutionize the established
analytical chemistry of the time and correspondingly revise the experi-
mental techniques with which pure elements were to be separated.®

1 Already mentioned above, pp. 128-9.

® Alas, all this is rational reconstruction rather than actual history. Prout denied the
existence of any anomalies. For instance, he claimed that the atomic weight of chlorine
was exactly 36.

3 Prout was aware of some of the basic methodological features of his programme.
Let us quote the first lines of his [1815]: “The author of the following essay submits it to
the public with the greatest diffidence... He trusts, however, that its importance will
be seen, and that some one will undertake to examine it, and thus verify or refute its con-
clusions. If these should be proved erroneous, still new facts may be brought to light,

or old ones better established, by the investigation; but if they should be verified, a new
and interesting light will be thrown upon the whole science of chemistry.’

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 139

Prout’s theory, as a matter of fact, defeated the theories previously applied
in purification of chemical substances one after the other. Even so, some
chemists became tired of the research programme and gave it up, since the
successes were still far from adding up to a final victory. For instance,
Stas, frustrated by some stubborn, recalcitrant instances, concluded in
1860 that Prout’s theory was ‘without foundations’.+ But others were more
encouraged by the progress than discouraged by the lack of complete
success. For instance, Marignac immediately retorted that ‘although [he
is satisfied that] the experiments of Monsieur Stas are perfectly exact,
[there is no proof] that the differences observed between his results and
those required by Prout’s law cannot be explained by the imperfect char-
acter of experimental methods’.? As Crookes put it in 1886: ‘Not a few
chemists of admitted eminence consider that we have here [in Prout’s
theory] an expression of the truth, masked by some residual or collateral
phenomena which we have not yet succeeded in eliminating.’® That is,
there had to be some further false hidden assumption in the ‘observa-
tional’ theories on which ‘experimental techniques’ for chemical purifica-
tion were based and with the help of which atomic weights were calcu-
lated: in Crookes’s view even in 1886 ‘some present atomic weights merely
represented a mean value’.* Indeed, Crookes went on to put this idea in a
scientific (content-increasing) form: he proposed concrete new theories of
‘fractionation’, a new ‘sorting Demon’.® But, alas, his new observational
theories turned out to be as false as they were bold and, being unable to
anticipate any new fact, they were eliminated from the (rationally recon-
structed) history of science. As it turned out a generation later, there was a
very basic hidden assumption which failed the researchers: that two pure
elements must be separable by chemical methods. The idea that two diff-
erent pure elements may behave identically in all chemical reactions but
can be separated by physical methods, required a change, a ‘stretching’, of
the concept of ‘pure element’ which constituted a change—a concept-
stretching expansion—of the research programme itself.6 This revolutionary
highly creative shift was taken only by Rutherford’s school’; and then ‘after

1 Clerk Maxwell was on Stas’s side: he thought it was impossible that there should be
two kinds of hydrogen, ‘for if some [molecules] were of slightly greater mass than others,
we have the means of producing a separation between molecules of different masses,
one of which would be somewhat denser than the other. As this cannot be done, we
must admit [that all are alike]’ (Maxwell [(1871]). ® Marignac [1860].

3 Crookes [1886]. 4 Ibid. 5 Crookes [1886], p. 491.

§ For ‘concept-stretching’, cf. my [1963-4], part IV.

7 The shift is anticipated in Crookes’s fascinating [1888] where he indicates that the
solution should be sought in a new demarcation between ‘physical’ and ‘chemical’, But
the anticipation remained philosophical; it was left to Rutherford and Soddy to develop
it, after 1910, into a scientific theory.

140 IMRE LAKATOS

many vicissitudes and the most convincing apparent disproofs, the hypo-
thesis thrown out so lightly by Prout, an Edinburgh physician, in 1815, has,
a century later, become the corner-stone of modern theories of the struc-
ture of atoms’.1 However, this creative step was in fact only a side-result
of progress in a different, indeed, distant research programme; Proutians,
lacking this external stimulus, never dreamt of trying, for instance, to
build powerful centrifugal machines to separate elements.

(When an ‘observational’ or ‘interpretative’ theory finally gets elimi-
nated, the ‘precise’ measurements carried out within the discarded frame-
work may look—with hindsight—rather foolish. Soddy made fun of
‘experimental precision’ for its own sake: “There is something surely akin
to if not transcending tragedy in the fate that has overtaken the life work of
that distinguished galaxy of nineteenth-century chemists, rightly revered
by their contemporaries as representing the crown and perfection of
accurate scientific measurement. Their hard won results, for the moment
at least, appears as of as little interest and significance as the determination
of the average weight of a collection of bottles, some of them full and some
of them more or less empty.’*)

Let us stress that in the light of the methodology of research pro-
grammes here proposed there never was any rational reason to eliminate
Prout’s programme. Indeed, the programme produced a beautiful, pro-
gressive shift, even if, in between, there were considerable hitches.? Our
sketch shows how a research programme can challenge a considerable bulk
of accepted scientific knowledge: it is planted, as it were, in an inimical
environment which, step by step, it can override and transform.

Also, the actual history of Prout’s programme illustrates only too well
how much the progress of science was hindered and slowed down by
justificationism and by naive falsificationism. (The opposition to atomic
theory in the nineteenth century was fostered by both.) An elaboration of
this particular influence of bad methodology on science may be a rewarding
research programme for the historian of science.

(c 2) Bohr: a research programme progressing on inconsistent foundations.
A brief sketch of Bohr’s research programme of light emission (in early
quantum physics) will illustrate further—and even expand—our thesis.*

1 Soddy [1932], p. 50. 2 Ibid.

3 These hitches inevitably induce many individual scientists to shelve or altogether
jettison the programme and join other research programmes where the positive heuristic
happens to offer at the time cheaper successes: the history of science cannot be fully
understood without mob-psychology. (Cf. below, pp. 177-80.)

4 This section may again strike the historian as more a caricature than a sketch; but I
hope it serves its purpose. (Cf. above, p. 138.) Some statements are to be taken not with a
grain, but with tons, of salt.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES I4I

The story of Bohr’s research programme can be characterized by: (1) its
initial problem; (2) its negative and positive heuristic; (3) the problems
which it attempted to solve in the course of its development; and (4) its
degeneration point (or, if you wish, ‘saturation point’) and, finally, (5) the
programme by which it was superseded.

The background problem was the riddle of how Rutherford atoms (that
is, minute planetary systems with electrons orbiting round a positive
nucleus) can remain stable; for, according to the well-corroborated
Maxwell—Lorentz theory of electromagnetism they should collapse. But
Rutherford’s theory was well corroborated too. Bohr’s suggestion was to
ignore for the time being the inconsistency and consciously develop a
research programme whose ‘refutable’ versions were inconsistent with the
Maxwell-Lorentz theory.1 He proposed five postulates as the hard core of
his programme: ‘(1) that energy radiation [within the atom] is not emitted
(or absorbed) in the continuous way assumed in the ordinary electro-
dynamics, but only during the passing of the systems between different
“stationary”’ states. (2) That the dynamical equilibrium of the systems in
the stationary states is governed by the ordinary laws of mechanics, while
these laws do not hold for the passing of the systems between the different
states. (3) That the radiation emitted during the transition of a system
between two stationary states is homogeneous, and that the relation
between the frequency v and the total amount of energy emitted F is given
by E = hv, where h is Planck’s constant. (4) That the different stationary
states of a simple system consisting of an electron rotating round a
positive nucleus are determined by the condition that the ratio between the
total energy, emitted during the formation of the configuration, and the
frequency of revolution of the electron is an entire multiple of 3. Assuming
that the orbit of the electron is circular, this assumption is equivalent with
the assumption that the angular momentum of the electron round the
nucleus is equal to an entire multiple of #/am. (5) That the “permanent”
state of any atomic system, i.e. the state in which the energy emitted is
maximum, is determined by the condition that the angular momentum of
every electron round the centre of its orbit is equal to h/27.”*

We have to appreciate the crucial methodological difference between the
inconsistency introduced by Prout’s programme and that introduced by
Bohr’s. Prout’s research programme declared war on the analytical chem-
istry of his time: its positive heuristic was designed to overthrow it and
replace it. But Bohr’s research programme contained no analogous design:

1 This, of course, is a further argument against J. O. Wisdom’s thesis that metaphysical
theories can be refuted by a conflicting well corroborated scientific theory (Wisdom
[1963]) Also, cf. above, p. 112, text to footnote 1, and pp. 126-7,

? Bohr [1913a], p. 874.

142 IMRE LAKATOS

its positive heuristic, even if it had been completely successful, would have
left the inconsistency with the Maxwell-Lorentz theory unresolved.! To
suggest such an idea required even greater courage than Prout’s; the idea
crossed Einstein’s mind but he found it unacceptable, and rejected it.?
Indeed, some of the most important research programmes in the history of
science were grafted on to older programmes with which they were blatantly
inconsistent, For instance, Copernican astronomy was ‘grafted’ on to Aris-
totelian physics, Bohr’s programme on to Maxwell’s. Such ‘grafts’ are
irrational for the justificationist and for the naive falsificationist, neither of
whom can countenance growth on inconsistent foundations. Therefore
they are usually concealed by ad hoc stratagems—like Galileo’s theory of
circular inertia or Bohr’s correspondence, and, later, complementarity
principle—the only purpose of which is to hide the ‘deficiency’.? As the
young grafted programme strengthens, the peaceful co-existence comes to
an end, the symbiosis becomes competitive and the champions of the new
programme try to replace the old programme altogether.

It may well have been the success of his ‘grafted programme’ which later
misled Bohr into believing that such fundamental inconsistencies in re-
search programmes can and should be put up with in principle, that they
do not present any serious problem and one merely has to get used to
them. Bohr tried in 1922 to lower the standards of scientific criticism; he
argued that ‘the most that one can demand of a theory [i.e. programme] is
that the classification [it establishes] can be pushed so far that it can
contribute to the development of the field of observation by the prediction
of new phenomena.”4

(This statement by Bohr is similar to d’Alembert’s when faced with the
inconsistency in the foundations of infinitesimal theory: ‘Allez en avant
et la foi vous viendra.’ According to Margenau, ‘it is understandable that,
in the excitement over its success, men overlooked a malformation in the
theory’s architecture; for Bohr’s atom sat like a baroque tower upon the
Gothic base of classical electrodynamics.’> But as a matter of fact, the
‘malformation’ was not ‘overlooked’: everybody was aware of it, only they
ignored it—more or less—during the progressive phase of the programme.®

1 Bohr held at this time that the Maxwell—Lorentz theory would eventually have to be
replaced (Einstein’s photon theory had already indicated this need).

2 Hevesy [1913]; cf. also above, p. 136, text to footnote 1.

3 In our methodology there is no need for such protective ad hoc stratagems. But, on
the other hand, they are harmless as long as they are clearly seen as problems, not as
solutions.

* Bohr [1922]; my italics.

5 Margenau [1950], p. 311.

6 Sommerfeld ignored it more than Bohr: cf. below, p. 150, footnote 4.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 143

Our methodology of research programmes shows the rationality of this
attitude but it also shows the irrationality of the defence of such ‘malfor-
mations’ once the progressive phase is over.

It should be said here that in the thirties and forties Bohr abandoned
his demand for ‘new phenomena’ and was prepared to ‘proceed with the
immediate task of co-ordinating the multifarious evidence regarding
atomic phenomena, which accumulated from day to day in the explora-
tion of this new field of knowledge’. This indicates that Bohr, by this time,
had fallen back on ‘saving the phenomena’, while Einstein sarcastically
insisted that ‘every theory is true provided that one suitably associates its
symbols with observed quantities’.*)

But consistency—in a strong sense of the term®—sust remain an impor-
tant regulative principle (over and above the requirement of progressive
problemshift); and inconsistencies must be seen as problems. The reason is
simple. If science aims at truth, it must aim at consistency; if it resigns
consistency, it resigns truth. To claim that ‘we must be modest in our
demands’,‘ that we must resign ourselves to—weak or strong—incon-
sistencies, remains a methodological vice. On the other hand, this does not
mean that the discovery of an inconsistency—or of an anomaly—must
immediately stop the development of a programme: it may be rational to
put the inconsistency into some temporary, ad hoc quarantine, and carry
on with the positive heuristic of the programme. This has been done even
in mathematics, as the examples of the early infinitesimal calculus and of
naive set theory show.®

1 Bohr [1949], p. 206.

2 Quoted in Schrédinger [1958], p. 170.

3 Two propositions are inconsistent if their conjunction has no model, that is, there is
no interpretation of their descriptive terms in which the conjunction is true. But in
informal discourse we use more formative terms than in formal discourse: some descriptive
terms are given a fixed interpretation. In this informal sense two propositions may be
(weakly) inconsistent given the standard interpretations of some characteristic terms even
if formally, in some unintended interpretation, they may be consistent. For instance,
the first theories of electron spin were inconsistent with the special theory of relativity
if ‘spin’ was given its (‘strong’) standard interpretation and thereby treated as a formative
term; but the inconsistency disappears if ‘spin’ is treated as an uninterpreted descriptive
term, The reason why we should not give up standard interpretations too easily is that
such emasculation of meanings may emasculate the positive heuristic of the programme.
(On the other hand, such meaning shifts may be in some cases progressive: cf. above, p.
126.)

For the shifting demarcation between formative and descriptive terms in informal
discourse, cf. my [1963-4], 9(b), especially p. 335, footnote 1.

* Bohr [1922], last paragraph. ‘

5 Naive falsificationists tend to regard this liberalism as a crime against reason. Their
main argument runs like this: ‘If one were to accept contradictions, then one would have
to give up any kind of scientific activity: it would mean a complete breakdown of science.
This can be shown by proving that if two contradictory statements are admitted, any

144 IMRE LAKATOS

(From this point of view, Bohr’s ‘correspondence principle’ played an
interesting double role in his programme. On the one hand it functioned
as an important heuristic principle which suggested many new scientific
hypotheses which, in turn, led to novel facts, especially in the field of the
intensity of spectrum lines.1 On the other hand it functioned also as a
defence-mechanism, which ‘endeavoured to utilize to the utmost extent
the concepts of the classical theories of mechanics and electrodynamics, in
spite of the contrast between these theories and the quantum of action’,”
instead of emphasizing the urgency of a unified programme. In this second
role it reduced the degree of problematicality of the programme.*)

Of course, the research programme of quantum theory as a whole was a
‘grafted programme’ and therefore repugnant to physicists with deeply
conservative views like Planck. There are two extreme and equally irra-
tional positions with regard to a grafted programme.

The conservative position is to halt the new programme until the basic
inconsistency with the old programme is somehow repaired: it is irrational
to work on inconsistent foundations. The ‘conservatives’ will concentrate
on eliminating the inconsistency by explaining (approximately) the postu-
lates of the new programme in terms of the old programme: they find it
irrational to go on with the new programme without a successful reduction
of the kind mentioned. Planck himself chose this way. He did not succeed,
in spite of the decade of hard work he invested in it.4 Therefore Laue’s
remark that his lecture on 14 December 1900, was the ‘birthday of the
quantum theory’ is not quite true: that day was the birthday of Planck’s
reduction programme. The decision to go ahead with temporarily incon-
sistent foundations was taken by Einstein in 1905, but even he wavered in
1913, when Bohr forged forward again.
statement whatever must be admitted; for from a couple of contradictory statements any
statement whatever can be validly inferred... A theory which involves a contradiction
is therefore entirely useless as a theory ’ (Popper [1940]). In fairness to Popper, one has
to stress that he is here arguing against Hegelian dialectic, in which inconsistency becomes
a virtue; and he is absolutely right when he points out its dangers. But Popper never
analysed patterns of empirical (or non-empirical) progress on inconsistent foundations;
indeed, in section 24 of his [1934] he makes consistency and falsifiability mandatory
requirements for any scientific theory. I discuss this problem in more detail in my [1970].

1Cf. e.g. Kramers [1923]. ? Bohr [1923].

3 Born, in his [1954], gives a vivid account of the correspondence principle which
strongly supports this double appraisal: ‘The art of guessing correct formulae, which

deviate from the classical ones, yet contain them as a limiting case... was brought to a
high degree of perfection.’

4¥For the fascinating story of this long series of frustrating failures, cf. Whittaker,
[1953], pp. 103-4. Planck himself gives a dramatic description of these years: ‘My futile
attempts to fit the elementary quantum of action into the classical theory continued for a
number of years, and they cost me a great deal of effort. Many of my colleagues saw in
this something bordering on a tragedy...’ (Planck [1947]).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 145

The anarchist position concerning grafted programmes is to extol
anarchy in the foundations as a virtue and regard [weak] inconsistency
either as some basic property of nature or as an ultimate limitation of
human knowledge, as some of Bohr’s followers did.

The rational position is best characterized by Newton’s, who faced a
situation which was to a certain extent similar to the one discussed, Car-
tesian push-mechanics, on which Newton’s programme was originally
grafted, was (weakly) inconsistent with Newton’s theory of gravitation.
Newton worked both on his positive heuristic (successfully) and on a re-
ductionist programme (unsuccessfully), and disapproved both of Car-
tesians who, like Huyghens, thought that it was not worth wasting time on
an ‘ unintelligible’ programme and of some of his rash disciples who, like
Cotes, thought that the inconsistency presented no problem.!

The rational position with regard to ‘grafted’ programmes is then to
exploit their heuristic power without resigning oneself to the fundamental
chaos on which it is growing. On the whole, this attitude dominated old,
pre-1925 quantum theory. In the new, post-1925 quantum theory the
‘anarchist’ position became dominant and modern quantum physics, in its
‘Copenhagen interpretation’, became one of the main standard bearers of
philosophical obscurantism. In the mew theory Bohr’s notorious ‘comple-
mentarity principle’ enthroned {weak] inconsistency as a basic factual final
feature of nature, and merged subjectivist positivism and _ antilogical
dialectic and even ordinary language philosophy into one unholy alliance.
After 1925 Bohr and his associates introduced a new and unprecedented
lowering of critical standards for scientific theories. This led to a defeat
of reason within modern physics and to an anarchist cult of incompre-
hensible chaos. Einstein protested: “The Heisenberg—Bohr tranquillizing
philosophy—or religion?—is so delicately contrived that, for the time
begin, it provides a gentle pillow for the true believer’. On the other hand,

1Cf. my [1970]. Of course, a reductionist programme is scientific only if it explains
more than it has set out to explain; otherwise the reduction is not scientific (cf. Popper
[1969]). If the reduction does not produce new empirical content, let alone novel facts,
then the reduction represents a degenerating problemshift—it is a mere linguistic
exercise. The Cartesian efforts to bolster up their metaphysics in order to be able to
interpret Newtonian gravitation in its terms, is an outstanding example for such merely
linguistic reduction. Cf. above, p. 126, footnote 2.

* Einstein [1928]. Among the critics of the Copenhagen ‘anarchism’ we should mention
—besides Einstein—Popper, Landé, Schrédinger, Margenau, Blokhinzev, Bohm, Fényes
and Janossy. For a defence of the Copenhagen interpretation, cf, Heisenberg [1955]; for a
hard-hitting recent criticism, cf. Popper [1967]. Feyerabend in his [1968-9], makes use
of some inconsistencies and waverings in Bohr’s position for'a crude apologetic falsification
of Bohr’s philosophy. Feyerabend misrepresents Popper’s, Landé’s and Margenau’s
critical attitude to Bohr, gives insufficient emphasis to Einstein’s opposition, and seems to
have forgotten completely that in some of his earlier papers he was more Popperian than
Popper on this issue.

146 IMRE LAKATOS

Einstein’s too high standards may well have been the reason that prevented
him for discovering (or perhaps only from publishing) the Bohr model
and wave mechanics.

Einstein and his allies have not won the battle. Physics textbooks are
nowadays full of statements like this: ‘The two viewpoints, quanta and
electromagnetic field strengths, are complementary in the sense of Bohr.
This complementarity is one of the great achievements of natural phil-
osophy in which the Copenhagen interpretation of the epistemology of
quantum theory has resolved the age-old conflict between the corpuscular
and the wave theories of light. From the reflection and rectilinear propa-
gation properties of Hero of Alexandria in the first century a.D., right
through to the interference and wave properties of Young and Maxwell
in the nineteenth century, this controversy raged. The quantum theory of
radiation during the past half century, in a striking Hegelian manner, has
completely resolved the dichotomy’ .1

Let us now return to the logic of discovery of old quantum theory and,
in particular, concentrate on its positive heuristic. Bohr’s plan was to work
out first the theory of the hydrogen atom. His first model was to be based
on a fixed proton-nucleus with an electron in a circular orbit; in his second
model he wanted to calculate an elliptical orbit in a fixed plane; then he
intended to remove the clearly artificial restrictions of the fixed nucleus
and fixed plane; after this he thought of taking the possible spin of the
electron into account,? and then he hoped to extend his programme to the
structure of complicated atoms and molecules and to the effect of electro-
magnetic fields on them, etc., etc. All this was planned right at the start:
the idea that atoms are analogous to planetary systems adumbrated a long,
difficult but optimistic programme and clearly indicated the policy of
research.’ ‘It looked at this time—in the year 1913—as if the authentic

1 Power [1964], p. 31 (my italics), ‘Completely’ is meant here literally. As we read in
Nature (222, 1969, pp. 1034-5): ‘It is absurd to think that any fundamental element of
(quantum] theory can be false... The arguments that scientific results are always tem-
porary, cannot hold. It is the philosophers’ conceptions of modern physics that are temporary,
because they have not yet realized how profoundly the discoveries of quantum physics
affect the whole of epistemology. ... The assertion that ordinary language is the ultimate
source of the unambiguousness of physical description is verified most convincingly by the
observational conditions in quantum physics.’

? This is rational reconstruction. As a matter of fact, Bohr accepted this idea only in
his [1926].

3 Besides this analogy, there was another basic idea in Bohr’s positive heuristic: the
‘correspondence principle’. This was indicated by him as early as 1913 (cf. the second of
his five postulates quoted above on p. 141), but he developed it only later when he used
it as a guiding principle in solving some problems of the later, sophisticated models (like
the intensities and states of polarization). The peculiarity of this second part of his positive
heuristic was that Bohr did not believe its metaphysical version: he thought it was a tem-
porary rule until the replacement of classical electromagnetics (and possibly mechanics).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 147

key to the spectra had at last been found, as if only time and patience would
be needed to resolve their riddles completely.’

Bohr’s celebrated first paper of 1913 contained the initial step in the
research programme. It contained his first model (I shall call it M,) which
already predicted facts hitherto unpredicted by any previous theory: the
wavelengths of hydrogen’s line emission spectrum. Though some of these
wavelengths were known before 1913—the Balmer series (1885) and the
Paschen series (1908)—Bohr’s theory predicted much more than these two
known series. And tests soon corroborated its novel content: one additional
Bohr series was discovered by Lyman in 1914, another by Brackett in
1922 and yet another by Pfund in 1924.

Since the Balmer and the Paschen series were known before 1913, some
historians present the story as an example of a Baconian ‘inductive ascent’:
(1) the chaos of spectrum lines, (2) an ‘empirical law’ (Balmer), (3) the theore-
tical explanation (Bohr). This certainly looks like the three ‘floors’ of Whewell.
But the progress of science would hardly have been delayed had we lacked
the laudible trials and errors of the ingenious Swiss school-teacher: the
speculative mainline of science, carried forward by the bold speculations
of Planck, Rutherford, Einstein and Bohr would have produced Balmer’s
results deductively, as test-statements of their theories, without Balmer’s
so-called ‘pioneering’. In the rational reconstruction of science there is
little reward for the pains of the discoverers of ‘naive conjectures’.?

As a matter of fact, Bohr’s problem was not to explain Balmer’s and
Paschen’s series, but to explain the paradoxical stability of the Rutherford
atom. Moreover, Bohr had not even heard of these formulae before he
wrote the first version of his paper.*

Not all the novel content of Bohr’s first model M4, was corroborated.
For instance, Bohr’s M, claimed to predict all the lines in the hydrogen
emission spectrum. But there was experimental evidence for a hydrogen

1 Davisson [1937]. A similar euphoria was experienced by MacLaurin in 1748 over
Newton’s programme: Newton’s ‘philosophy being founded on experiment and demonstra-
tion, cannot fail till reason or the nature of things are changed . . . [Newton] left to posterity
little more to do, but observe the heavens, and compute after his models’ (MacLaurin
[1748], p. 8).

2 T use here ‘naive conjecture’ as a technical term in the sense of my [1963-4]. For a case
study and detailed criticism of the myth of the ‘inductive basis’ of science (natural or
mathematical) cf. ibid. section 7, especially pp. 298~307. There I show that Descartes’s and
Euler’s ‘naive conjecture’ that for all polyhedra V— E+ F = 2 was irrelevant and superfluous
for the later development; as further examples one may mention that Boyle’s and his
successors’ labours to establish pv = RT was irrelevant for the later theoretical development
(except for developing some experimental techniques), as Kepler’s three laws may have
been superfluous for the Newtonian theory of gravitation.

For further discussion of this point cf. below, p. 175.

3 Cf. Jammer [1966], pp. 77 ff.

148 IMRE LAKATOS

series where according to Bohr’s M, there should have been none. The
anomalous series was the Pickering—Fowler ultraviolet series.

Pickering discovered this series in 1896 in the spectrum of the star
¢ Puppis. Fowler, after having discovered its first line also in the sun in
1898, produced the whole series in a discharge tube containing hydrogen
and helium. True, it could be argued that the monster-line had nothing
to do with the hydrogen—after all, the sun and ¢ Puppis contain many
gases and the discharge tube also contained helium. Indeed, the line could
not be produced in a pure hydrogen tube. But Pickering’s and Fowler’s
‘experimental technique’, that led to a falsifying hypothesis of Balmer’s
law, had a plausible, although never severely tested, theoretical back-
ground: (a) their series had the same convergence number as the Balmer
series and therefore was taken to be a hydrogen series and (b) Fowler gave
a plausible explanation why helium could not possibly be responsible for
producing the series.!

Bohr was not, however, very impressed by the ‘authoritative’ experi-
mental physicists. He did not question their ‘experimental precision’ or
the ‘reliability of their observations’, but questioned their observational
theory. Indeed, he proposed an alternative. He first elaborated a new
model (M,) of his research programme: the model of ionized helium, with
a double proton orbited by an electron. Now this model predicts an ultra-
violet series in the spectrum of ionized helium which coincides with the
Pickering-Fowler series. This constituted a rival theory. Then he sug-
gested a ‘crucial experiment’: he predicted that Fowler’s series can be
produced, possibly with even stronger lines, in a tube which is filled with a
mixture of helium and chlorine. Moreover, Bohr explained to the experi-
mentalists, without even looking at their apparatus, the catalytic role of the
hydrogen in Fowler’s experiment and of chlorine in the experiment he
suggested.” Indeed, he was right.* Thus the first apparent defeat of the
research programme was turned into a resounding victory.

1 Fowler [1912]. Incidentally his ‘observational’ theory was provided by ‘Rydberg’s
theoretical investigations’ which ‘in the absence of strict experimental proof [he] regarded
as justifying [his experimental] conclusion’ (p. 65). But his theoretician colleague, Pro-
fessor Nicholson, referred three months later to Fowler’s findings as ‘laboratory confirma-
tions of Rydberg’s theoretical deduction’ (Nicholson [1913]). This little story, I think,
bears out my pet thesis that most scientists tend to understand little more about science
than fish about hydrodynamics,

In the Report of the Council to the Ninety-third Annual General Meeting of the Royal
Astronomical Society, Fowler’s ‘observation in laboratory experiments’ of new ‘hydrogen
lines which have so long eluded the efforts of the physicists’ is described as ‘an advance of
great interest’ and as ‘a triumph of well-directed experimental work’. ? Bohr [19136].

3 Evans [1913]. For a similar example of a theoretical physicist teaching a refutation-

keen experimentalist what he—the experimentalist—had really observed, cf. above, p. 130,
footnote 5.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 149

The victory, however, was immediately questioned. Fowler acknow-
ledged that his series was not a hydrogen, but a helium series. But he
pointed out that Bohr’s monster-adjustment! still failed: the wavelengths
in the Fowler series differ significantly from the values predicted by Bohr’s
M,. Thus the series, although it does not refute M,, still refutes M, and
because of the close connection between M, and M,, it undermines M,!?

Bohr brushed off Fowler’s argument: of course he never meant M, to be
taken too seriously. His values were based on a crude calculation basedonthe
electron orbiting round a fixed nucleus; but ofcourse it orbits round the com-
mon centre of gravity; of course, as is done when treating two-body pro-
blems, one has to substitute reduced mass for mass: m; — me/[1-+(me/m,)}.°
This modified model was Bohr’s Mj. And Fowler himself had to admit
that Bohr was again right.4

The apparent refutation of M, turned into a victory for M,; and it was
clear that M, and M, would have been developed within the research pro-
gramme—perhaps even M,, or M,)—without any stimulus from observa-
tion or experiment. It was at this stage that Einstein said of Bohr’s theory:
‘It is one of the greatest discoveries.’®

Bohr’s research programme then went on as planned. The next step
was to calculate elliptical orbits. This was done by Sommerfeld in 1915,
but with the (unexpected) result that the increased number of possible
steady orbits did ot increase the number of possible energy levels, so
there seemed to be no possibility of a crucial experiment between the
elliptical and circular theory. However, electrons orbit the nucleus with
very high velocity so that when they accelerate their mass should change
noticeably if Einsteinian mechanics is true. Indeed, calculating such rela-
tivistic corrections, Sommerfeld got a new array of energy levels and thus the
‘finestructure’ of the spectrum.

The switch to this new relativistic model required much more mathe-
matical skill and talent than the development of the first few models.
Sommerfeld’s achievement was primarily mathematical.®

1 Monster-adjustment: turning a counterexample, in the light of some new theory, into
an example. Cf. my [1963-4], pp. 127 ff. But Bohr’s ‘monster-adjustment’ was empirically
‘progressive’: it predicted a new fact (the appearance of the 4686 line in tubes containing
no hydrogen). ? Fowler [1913a].

’ Bohr [1913c]. This monster-adjustment was also ‘progressive’: Bohr predicted that
Fowler’s observations must be slightly imprecise and the Rydberg ‘constant’ must have a
fine structure.

4 Fowler [19136]. But he sceptically noted that Bohr’s programme had not yet explained
the spectrum lines of un-ionized, ordinary helium. However, he soon abandoned his
scepticism and joined Bohr’s research programme (Fowler [1914]).

5 Cf. Hevesy [1913]: “When I told him of the Fowler spectrum, the big eyes of Einstein
looked still bigger and he told me: “Then it is one of the greatest discoveries.” ’

8 For the vital mathematical aspects of research programmes, cf. above, p. 137.

150 IMRE LAKATOS

Curiously, the doublets of the hydrogen spectrum had already been dis-
covered in 1891 by Michelson.! Moseley pointed out immediately after
Bohr’s first publication that ‘it fails to account for the second weaker line
found in each spectrum’. Bohr was not upset: he was convinced that the
positive heuristic of his research programme would, im due course, explain
and even correct Michelson’s observations.® And so it did. Sommerfeld’s
theory was, of course, inconsistent with Bohr’s first versions; the fine-
structure experiments—with the old observations corrected !—provided
the crucial evidence in its favour. Many defeats of Bohr’s first models were
turned by Sommerfeld and his Munich school into victories for Bohr’s
research programme.

It is interesting that just as Einstein got worried and slowed down in the
middle of the spectacular progress of quantum physics by 1913, Bohr got
worried and slowed down by 1916; and just as Bohr had, by 1913 taken
the initiative from Einstein, Sommerfeld had taken the initiative from
Bohr by 1916. The difference between the atmosphere of Bohr’s Copen-
hagen school and Sommerfeld’s Munich school was conspicuous: ‘In
Munich one used more concrete formulations and was therefore more
easily understood; one had been successful in the systematization of
spectra and in the use of the vector model. In Copenhagen, however, one
believed that an adequate language for the new [phenomena] had not yet
been found, one was reticent in the face of too definite formulations, one
expressed oneself more cautiously and more in general terms, and was
therefore much more difficult to understand.’4

Our sketch shows how a progressive shift may lend credibility—and
rationale—to an inconsistent programme. Born, in his obituary of Planck,
describes this process forcefully: ‘Of course the mere introduction of the
quantum of action does not yet mean that a true Quantum Theory has
been established ... The difficulties which the introduction of the quan-
tum of action into the well-established classical theory has encountered
from the outset have already been indicated. They have gradually in-
creased rather than diminished; and although research in its forward
march has in the meantime passed over some of them, the remaining gaps

1 Michelson [1891-2], especially pp. 287-9. Michelson does not even mention Balmer.

3 Moseley [1914].

3 Sommerfeld [1916], p. 68.

¢ Hund [1961]. This is discussed at some length in Feyerabend [1968-9], pp. 83-7
But Feyerabend’s paper is heavily biased. The main aim of his paper is to play down Bohr’s
methodological anarchism and show that Bohr opposed the Copenhagen interpretation of the
new (post-1925) quantum programme. In order to do so, Feyerabend, on the one hand,
overemphasizes Bohr’s unhappiness about the inconsistency of the old (pre-1925) quantum

programme and, on the other hand, makes too much of the fact that Sommerfeld cared less
for the problematicality of the inconsistent foundations of the old programme than Bohr.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES I51

in the theory are the more distressing to the conscientious theoretical
physicist. In fact, what in Bohr’s theory served as the basis of the laws
of action consists of certain hypotheses which a generation ago would
doubtless have been flatly rejected by every physicist. That within the atom
certain quantized orbits (i.e. picked out on the quantum principle) should
play a special role could well be granted; somewhat less easy to accept is
the further assumption that the electrons moving on these curvilinear
orbits, and therefore accelerated, radiate no energy. But that the sharply
defined frequency of an emitted light quantum should be different from
the frequency of the emitting electron would be regarded by a theore-
tician who had grown up in the classical school as monstrous and almost
inconceivable. But numbers [or, rather, progressive problemshifts] decide,
and in consequence the tables have been turned. While originally it was a
question of fitting in with as little strain as possible a new and strange
element into an existing system which was generally regarded as settled,
the intruder, after having won an assured position, now has assumed the
offensive; and it now appears certain that it is about to blow up the old
system at some point. The only question now is, at what point and to what
extent this will happen.”?

One of the most important points one learns from studying research
programmes is that relatively few experiments are really important. The
heuristic guidance the theoretical physicist receives from tests and ‘refuta-
tions’ is usually so trivial that large-scale testing—or even bothering too
much with the data already available—may well be a waste of time. In
most cases we need no refutations to tell us that the theory is in urgent
need of replacement: the positive heuristic of the programme drives us
forward anyway. Also, to give a stern ‘refutable interpretation’ to a fledgling
version of a programme is dangerous methodological cruelty. The first
versions may even ‘apply’ only to non-existing ‘ideal’ cases; it may take
decades of theoretical work to arrive at the first novel facts and still more
time to arrive at interestingly testable versions of the research programmes,
at the stage when refutations are no longer forseeable in the light of the
programme itself.

The dialectic of research programmes is then not necessarily an alter-
nating series of speculative conjectures and empirical refutations. The
interaction between the development of the programme and the empirical
checks may be very varied—which pattern is actually realized depends only
on historical accident. Let us mention three typical variants.

(1) Let us imagine that each of the first three consecutive versions, H.

1
H,, H; predict some new facts successfully but others unsuccessfully, that is

1 Born [1948], p. 180; my italics.

1§2 IMRE LAKATOS

each version is both corroborated and refuted in turn. Finally H, is pro-
posed which predicts some novel facts but stands up to the severest tests.
The problemshift is progressive, and also we have a beautiful Popperian
alternation of conjectures and refutations.1 People will admire this as a
classical example of theoretical and experimental work going hand in
hand.

(2) Another pattern could have been a lone Bohr (possibly without
Balmer preceding him), working out H,, H,, H, H, but self-critically
withholding publication until H,. Then H, is tested: all the evidence will
turn up as corroborations of H,, the first (and only) published hypothesis.
The theoretician—at his desk—is here seen to work far ahead of the
experimenter: we have a period of relative autonomy of theoretical pro-
gress.

(3) Let us now imagine that all the empirical evidence mentioned in
these three patterns is already there at the time of the invention of H,, H,,
Hy, H,. In this case H,, Hy, H 3, H, will not represent an empirically pro-
gressive problemshift and therefore, although all the evidence supports
his theories, the scientist has to work on further in order to prove the
scientific value of his programme.* Such a state of affairs may be brought
about either by the fact that an older research programme (which has
been challenged by the one leading to H,, Hy, Hs, Hy) had already pro-
duced all these facts—or by the fact that too much government money lay
around for collecting data about spectrum lines and hacks stumbled upon
all the data. However the latter case is extremely unlikely, for, as Cullen
used to say, ‘the number of false facts, afloat in the world, infinitely
exceeds that of the false theories’*; in most such cases the research pro-
gramme will clash with the available ‘facts’, the theoretician will look into
the ‘experimental techniques’ of the experimentalist, and having over-
thrown and replaced his observational theories will correct his facts
thereby producing novel ones.*

1 In the first three patterns we do not involve complications like successful appeals against
the verdict of the experimental scientists.

2 This shows that if exactly the same theories and the same evidence is rationally re-
constructed in different time orders, they may constitute either a progressive or a degenera-
tive shift. Also cf. my [1968a], p. 387.

3 Cf. McCulloch [1825], p. 21. For a strong argument on how extremely unlikely such a
pattern is, see below, pp. 156-7.

4 Perhaps it should be mentioned that manic data collection—and ‘too much’ precision
—prevents even the formation of naive ‘empirical’ hypotheses like Balmer’s. Had Balmer
known of Michelson’s fine-spectra, would he have ever found his formula? Or, had Tycho
de Brahe’s data been more precise, would Kepler’s elliptical law ever have been put forward?
The same applies to the naive first version of the general gas law, etc. The Descartes—Euler
conjecture on polyhedra might never have been made but for the scarcity of data; cf. my

[1963-4], pp. 298 ff.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 153

After this methodological excursion, let us return to Bohr’s programme.
Not all developments in the programme were foreseen and planned when
the positive heuristic was first sketched. When some curious gaps appeared
in Sommerfeld’s sophisticated models (some predicted lines never did
appear), Pauli proposed a deep auxiliary hypothesis (his ‘exclusion prin-
ciple’) which accounted not only for the known gaps but reshaped the
shell theory of the periodic system of elements and anticipated facts then
unknown.

I do not wish to give here an elaborate account of the development of
Bohr’s programme. But its detailed study from the methodological view-
point is a veritable goldmine: its marvellously fast progress—on incon-
sistent foundations!—was breathtaking, the beauty, originality and
empirical success of its auxiliary hypotheses, put forward by scientists of
brilliance and even genius, was unprecedented in the history of physics.
Occasionally the next version of the programme required only a trivial
improvement, like the replacement of mass by reduced mass. Occasionally,
however, to arrive at the next version required new sophisticated mathe-
matics, like the mathematics of the many-body problem, or new sophisti-
cated physical auxiliary theories. The additional mathematics or physics
was either dragged in from some part of extant knowledge (like relativity
theory) or invented (like Pauli’s exclusion principle). In the latter case we
have a ‘creative shift’ in the positive heuristic.

But even this great programme came to a point where its heuristic
power petered out. Ad hoc hypotheses multiplied and could not be replaced
by content-increasing explanations. For instance, Bohr’s theory of mole-
cular (band) spectra predicted the following formula for diatomic mole~-
cules:

h
v= gz [lm-+1)— ml

But the formula was refuted. Bohrians replaced the term m? by m(m+1):
this fitted the facts but was sadly ad hoc.

Then came the problem of some unexplained doublets in alkali spectra.
Landé explained them in 1924 by an ad hoc ‘relativistic splitting rule’,
Goudsmit and Uhlenbeck in 1925 by electron spin. If Landé’s explanation
was ad hoc, Goudsmit’s and Uhlenbeck’s was also inconsistent with special
relativity theory: surface points on the largish electron had to travel

1 ‘Between the appearance of Bohr’s great trilogy in 1913 and the advent of wave mechanics
in 1925, a large number of papers appeared developing Bohr’s ideas into an impressive
theory of atomic phenomena. It was a collective effort and the names of the physicists con-
tributing to it make up an imposing roll-call: Bohr, Born, Klein, Rosseland, Kramers,
Pauli, Sommerfeld, Planck, Einstein, Ehrenfest, Epstein, Debye, Schwarzschild,
Wilson ...’ (Ter Haar [1967], p. 43).

154 IMRE LAKATOS

faster than light, and the electron had even to be bigger than the whole
atom.1 Considerable courage was needed to propose it. (Kronig got the
idea earlier but refrained from publishing it because he thought it was
inadmissible.)

But temerity in proposing wild inconsistencies did not reap any more
rewards, The programme lagged behind the discovery of ‘facts’. Undigested
anomalies swamped the field. With ever more sterile inconsistencies and
ever more ad hoc hypotheses, the degenerating phase of the research
programme had set in: it started—to use one of Popper’s favourite phrases
—‘to lose its empirical character’.? Also many problems, like the theory of
perturbations, could not even be expected to be solved within it. A rival
research programme soon appeared: wave mechanics. Not only did the
new programme, even in its first version (de Broglie, 1924), explain
Planck’s and Bohr’s quantum conditions; it also led to an exciting new fact,
to the Davisson—Germer experiment. In its later, ever more sophisticated
versions it offered solutions to problems which had been completely out
of the reach of Bohr’s research programme, and explained the ad hoc later
theories of Bohr’s programme by theories satisfying high methodological
standards. Wave mechanics soon caught up with, vanquished and replaced
Bohr’s programme.

De Broglie’s paper came at the time when Bohr’s programme was de-
generating. But this was mere coincidence. One wonders what would have
happened if de Broglie had written and published his paper in 1914
instead of 1924.

(d) A new look at crucial experiments: the end of instant rationality.

It would be wrong to assume that one must stay witharesearch programme
until it has exhausted all its heuristic power, that one must not introduce a
rival programme before everybody agrees that the point of degeneration
has probably been reached. (Although one can understand the irritation of
a physicist when, in the middle of the progressive phase of a research pro-
gramme, he is confronted by a proliferation of vague metaphysical theories

1 A footnote in their paper reads: ‘It should be observed that [according to our theory]
the peripheral velocity of the electron would considerably exceed the velocity of light’
(Uhlenbeck and Goudsmit [1925)]). 2 Jammer [1966], pp. 146-8 and 151.

3 For a vivid description of this degenerating phase of Bohr’s programme, cf. Margenau
[1950], pp. 311-3.

In the progressive phase of a programme the main heuristic stimulus comes from the
positive heuristic: anomalies are largely ignored. In the degenerating phase the heuristic
power of the programme peters out. In the absence of a rival programme this situation
may be reflected in the psychology of the scientists by an unusual hypersensitivity to
anomalies and by a feeling of a Kuhnian ‘crisis’.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 155

stimulating no empirical progress.!) One must never allow a research
programme to become a Weltanschauung, or a sort of scientific rigour,
setting itself up as an arbiter between explanation and non-explanation, as
mathematical rigour sets itself up as an arbiter between proof and non-
proof. Unfortunately this is the position which Kuhn tends to advocate:
indeed, what he calls ‘normal science’ is nothing but a research programme
that has achieved monopoly. But, as a matter of fact, research programmes
have achieved complete monopoly only rarely and then only for relatively
short periods, in spite of the efforts of some Cartesians, Newtonians and
Bohrians. The history of science has been and should be a history of competing
research programmes (or, if you wish, ‘paradigms’), but it has not been and
must not become a succession of periods of normal science: the sooner com-
petition starts, the better for progress. “Theoretical pluralism’ is better than
‘theoretical monism’: on this point Popper and Feyerabend are right and
Kuhn is wrong.”

The idea of competing scientific research programmes leads us to the
problem: how are research programmes eliminated? It has transpired from
our previous considerations that a degenerating problemshift is no more a
sufficient reason to eliminate a research programme than some old-
fashioned ‘refutation’ or a Kuhnian ‘crisis’, Can there be any objective (as
opposed to socio-psychological) reason to reject a programme, that ts, to
eliminate tts hard core and its programme for constructing protective belts?
Our answer, in outline, is that such an objective reason is provided by a
rival research programme which explains the previous success of its rival
and supersedes it by a further display of heuristic power.?

However, the criterion of ‘heuristic power’ strongly depends on how we
construe ‘factual novelty’. Until now we have assumed that it is immed-~
iately ascertainable whether a new theory predicts a novel fact or not.* But
the novelty of a factual proposition can frequently be seen only after a long
period has elapsed. In order to show this, I shall start with an example.

1 This is what must have irritated Newton most in the ‘sceptical proliferation of theories’
by Cartesians. Cf. my [1970].

2 Nevertheless there is something to be said for at least some people sticking to a research
programme until it reaches its ‘saturation point’; a new programme is then challenged to
account for the full success of the old. It is no argument against this that the rival may,
when it was first proposed, already have explained all the success of the first programme;
the growth of a research programme cannot be predicted—it may stimulate important
unforeseeable auxiliary theories of its own. Also, if a version An of a research programme
P, is mathematically equivalent to a version Am of a rival P;, one should develop both:
their heuristic strength can still be very different.

3 I use ‘heuristic power’ here as a technical term to characterize the power of a research
programme to anticipate theoretically novel facts in its growth. I could of course use
‘explanatory power’: cf. above, p. 119, footnote 1.

* Cf. above, p. 116, text to footnote 2, and p. 134, text to footnote 3.

156 IMRE LAKATOS

Bohr’s theory logically implied Balmer’s formula for hydrogen lines as a
consequence. Was this a novel fact? One might have been tempted to
deny this, since after all, Balmer’s formula was well-known. But this is a
half-truth. Balmer merely ‘observed’ B,: that hydrogen lines obey the
Balmer formula. Bohr predicted B,: that the differences in the energy levels
in different orbits of the hydrogen electron obey the Balmer formula. Now one
may say that B, already contains all the purely ‘observational’ content of
B,. But to say this presupposes that there can be a pure ‘observational
level’, untainted by theory, and impervious to theoretical change. In fact,
B, was accepted only because the optical, chemical and other theories
applied by Balmer were well corroborated and accepted as interpretative
theories; and these theories could always be questioned. It might be argued
that we can ‘purge’ even B, of its theoretical presuppositions, and arrive
at what Balmer really ‘observed’, which might be expressed in the more
modest assertion, By: that the lines emitted in certain tubes in certain well-
specified circumstances (or in the course of a ‘controlled experiment’*) obey the
Balmer formula. Now some of Popper’s arguments show that we can never
arrive at any hard ‘observational’ rock-bottom in this way; ‘observational’
theories can easily be shown to be involved in By.3 On the other hand, given
that Bohr’s programme after a long progressive development, had shown its
heuristic power, its hard core would itself have become well corroborated*
and therefore qualified as an ‘observational’ or interpretative theory. But
then B, will be seen not as a mere theoretical reinterpretation of B,, but
as a new fact in its own right.

These considerations lend new emphasis to the hindsight element in our
appraisals and lead to a further liberalization of our standards. A new
research programme which has just entered the competition may start by
explaining ‘old facts’ in a novel way but may take a very long time before
it is seen to produce ‘genuinely novel’ facts. For instance, the kinetic
theory of heat seemed to lag behind the results of the phenomenological

1Cf. above, p. 147.

2 Cf. above, p. 111, footnote 6.

3 One of Popper’s arguments is particularly important: “There is a widespread belief
that the statement “‘I see that this table here is white’, possesses some profound advantage
over the statement “This table here is white”, from the point of view of epistemology.
But from the point of view of evaluating its possible objective tests, the first statement, in
speaking about me, does not appear more secure than the second statement, which speaks
about the table here’ ([1934], section 27). Neurath makes a characteristically blockheaded
comment on this passage: ‘For us such protocol statements have the advantage of having
more stability. One may retain the statement: ‘“‘People in the 16th century saw fiery swords
in the sky” while crossing out ‘There were fiery swords in the sky’”’’ (Neurath [1935], p. 362).

* This remark, incidentally, defines a ‘degree of corroboration’ for the ‘irrefutable’ hard cores

of research programmes. Newton’s theory (in isolation) had no empirical content, yet it was,
in this sense, highly corroborated.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 157

theory for decades before it finally overtook it with the Einstein-Smolu-
chowski theory of Brownian motion in 1905. After this, what had pre-
viously seemed a speculative reinterpretation of old facts (about heat, etc.)
turned out to be a discovery of novel facts (about atoms).

All this suggests that we must not discard a budding research programme
simply because it has so far failed to overtake a powerful rival. We should not
abandon it if, supposing its rival were not there, it would constitute a pro-
gressive problemshift.1 And we should certainly regard a newly interpreted
fact as a new fact, ignoring the insolent priority claims of amateur fact col-
lectors. As long as a budding research programme can be rationally reconstructed
as a progressive problemshift, it should be sheltered for a while from a powerful
established rival?

These considerations, on the whole, stress the importance of method-
ological tolerance, and leave the question of how research programmes are
eliminated still unanswered. The reader may even suspect that laying this
much stress on fallibility liberalizes or, rather, softens up, our standards to
the extent that we will be landed with radical scepticism. Even the cele-
brated ‘crucial experiments’ will then have no force to overthrow a research
programme; anything goes.®

But this suspicion is unfounded. Within a research programme ‘minor
crucial experiments’ between subsequent versions are quite common.
Experiments easily ‘decide’ between the n-th and 2+ 1-th scientific version,
since the 2-+ 1-th is not only inconsistent with the -th, but also supersedes
it. If the #+-1-th version has more corroborated content in the light of the
same programme and in the light of the same well corroborated observa-
tional theories elimination is a relatively routine affair (only relatively, for
even here this decision may be subject to appeal). Appeal procedures too
are occasionally easy: in many cases the challenged observational theory,
far from being well corroborated, is in fact an inarticulate, naive, ‘hidden’
assumption; it is only the challenge which reveals the existence of this
hidden assumption, and brings about its articulation, testing and downfall.
Time and again, however, the observational theories are themselves
embedded in some research programme and then the appeal procedure

1 Incidentally, in the methodology of research programmes, the pragmatic meaning of
‘rejection’ [of a programme] becomes crystal clear: it means the decision to cease working on
it.

2 Some might regard—cautiously—this sheltered period of development as ‘prescientific’
(or ‘theoretical’); and be prepared only when it starts producing ‘genuinely novel” facts to
recognize its truly scientific (or ‘empirical’) character—but then their recognition will have
to be retroactive.

3 Incidentally, this conflict between fallibility and criticism can be rightly said to be the
main problem—and driving force—of the Popperian research programme in the theory of

knowledge.

158 IMRE LAKATOS

leads to a clash between two research programmes: in such cases we may
need a ‘major crucial experiment’.

When two research programmes compete, their first ‘ideal’ models
usually deal with different aspects of the domain (for example, the first
model of Newton’s semi-corpuscular optics described light-refraction, the
first model of Huyghens’s wave optics light-interference). As the rival
research programmes expand, they gradually encroach on each other’s
territory and the m-th version of the first will be blatantly, dramatically
inconsistent with the m-th version of the second.’ An experiment is
repeatedly performed, and as a result, the first is defeated in this battle,
while the second wins. But the war is not over: any research programme
is allowed a few such defeats. All its needs for a comeback is to produce an
n-+-1-th (or 2+-k-th) content-increasing version and a verification of some
of its novel content.

If such a comeback, after sustained effort, is not forthcoming, the war
is lost and the original experiment is seen, with hindsight, to have been
‘crucial’, But especially if the defeated programme is a young, fast-de-
veloping programme, and if we decide to give sufficient credit to its ‘pre-
scientific’ successes, allegedly crucial experiments dissolve one after the
other in the wake of its forward surge. Even if the defeated programme is an
old, established and ‘tired’ programme, near its ‘natural saturation point’ ,?
it may continue to resist for a long time and hold out with ingenious
content-increasing innovations even if these are unrewarded with empirical
success. It is very difficult to defeat a research programme supported by
talented, imaginative scientists. Alternatively, stubborn defenders of the
defeated programme may offer ad hoc explanations of the experiments or a
shrewd ad hoc ‘reduction’ of the victorious programme to the defeated one.
But such efforts we should reject as unscientific.®

Our considerations explain why crucial experiments are seen to be crucial
only decades later. Kepler’s ellipses were generally admitted as crucial
evidence for Newton and against Descartes only about one hundred years
after Newton’s claim. The anomalous behaviour of Mercury’s perihelion

1 An especially interesting case of such competition is competitive symbiosis, when a
new programme is grafted on to an old one which is inconsistent with it; cf. above, p. 142

? There is not such thing as a natural ‘saturation point’; in my [1963-4], especially on
pp. 327-8, I was more of a Hegelian, and I thought there was; now I use the expression
with an ironical emphasis. There is no predictable or ascertainable limitation on human
imagination in inventing new, content-increasing theories or on the ‘cunning of reason’
(List der Vernunft) in rewarding them with some empirical success even if they are false
or even if the new theory has less verisimilitude—in Popper’s sense—than its predecessor.
(Probably all scientific thearies ever uttered by men will be false: they still may be rewarded

by empirical successes and even have increasing verisimilitude.)
® For an example, cf. above, p. 126, footnote 2.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 159

was known for decades as one of the many yet unsolved difficulties in
Newton’s programme; but only the fact that Einstein’s theory explained it
better transformed a dull anomaly into a brilliant ‘refutation’ of Newton’s
research programme.? Young claimed that his double-slit experiment of
1802 was a crucial experiment between the corpuscular and the wave pro-
grammes of optics; but his claim was only acknowledged much later, after
Fresnel developed the wave programme much further ‘progressively’ and
it became clear that the Newtonians could not match its heuristic power.
The anomaly, which had been known for decades, received the honorific
title of refutation, the experiment the honorific title of ‘crucial experiment’
only after a long period of uneven development of the two rival pro-
grammes. Brownian motion was for nearly a century in the middle of the
battlefield before it was seen to defeat the phenomenological research
programme and turn the war in favour of the atomists. Michelson’s ‘refu-
tation’ of the Balmer series was ignored for a generation until Bohr’s
triumphant research programme backed it up.

It may be worthwhile to discuss in detail some examples of experiments
whose ‘crucial’ character became evident only retrospectively. First I shall
take the celebrated Michelson—Morley experiment of 1887 which allegedly
falsified the ether theory and ‘led to the theory of relativity’, then the
Lummer-Pringsheim experiments which allegedly falsified the classical
theory of radiation and ‘led to the quantum theory’.? Finally I shall discuss
an experiment which many physicists thought would turn out to decide
against the conservation laws but which, in fact, ended up as their most
triumphant corroboration.

(d 1) The Michelson—Morley experiment.

Michelson first devised an experiment in order to test Fresnel’s and
Stokes’s contradictory theories about the influence of the motion of the
earth on the ether,® during his visit to Helmholtz’s Berlin institute in
1881. According to Fresnel’s theory, the earth moves through an ether at
rest, but the ether within the earth is partially carried along with the earth;
Fresnel’s theory therefore entailed that the velocity of the ether outside the

1 Thus an anomaly in a research programme is a phenomenon which we regard as something
to be explained in terms of the programme. More generally, we may speak, following Kuhn,
about ‘puzzles’: a ‘puzzle’ in a programme is a problem which we regard as a challenge to that
particular programme. A ‘puzzle’ can be resolved in three ways: by solving it within the original
programme (the anomaly turns into an example); by neutralizing it, i.e. solving it within an
independent, different programme (the anomaly disappears), or, finally, by solving it within
a rival programme (the anomaly turns into a counterexample).

2 Cf. Popper [1934], section 30.

3Cf. Fresnel [1818], Stokes [1845] and [1846]. For an excellent brief exposition cf,

Lorentz [1895].

160 IMRE LAKATOS

earth relative to the earth was positive (i.e. Fresnel’s theory implied the ex-
istence of an ‘ether wind’). According to Stokes’s theory, the ether
was dragged along by the earth and immediately on the surface of the
earth, the velocity of the ether was equal to that of the earth: therefore its
relative velocity was zero (i.e. there was no ether wind on the surface).
Stokes originally thought that the two theories were observationally
equivalent: for instance, with suitable auxiliary assumptions both theories
explained the aberration of light. But Michelson claimed that his 1881
experiment was a crucial experiment between the two and that it proved
Stokes’s theory. He claimed that the velocity of the earth relative to the
ether is far less than Fresnel’s theory would have it. Indeed, he concluded
that from his experiment' ‘the necessary conclusion follows that the hypo-
thesis [of a stationary ether] is erroneous. This conclusion directly con-
tradicts the explanation of the phenomenon of aberrration which . . . pre-
supposes that the earth moves through the ether, the latter remaining at
rest’.? As often happens, Michelson the experimenter was then taught a
lesson by a theoretician. Lorentz, the leading theoretical physicist of the
period, in what Michelson later described as ‘a very searching analysis...
of the entire experiment’,? showed that Michelson ‘misinterpreted’ the
facts and that what he observed did ot in fact contradict the hypothesis of
the stationary ether. Lorentz showed that Michelson’s calculations were
wrong; Fresnel’s theory predicted only half of the effect Michelson had
calculated. Lorentz concluded that Michelson’s experiment did not refute
Fresnel’s theory, and that it certainly did not prove Stokes’s theory either.
Lorentz went on to show that Stokes’s theory was inconsistent: that it
assumed the ether at the earth’s surface to be at rest with regard to the
latter and required that the relative velocity have a potential; but these
two conditions are incompatible. But even if Michelson had refuted one
theory of the stationary ether, the programme is untouched: one can easily
devise several other versions of the ether programme, which predict very
small values for the ether winds and he, Lorentz, immediately produced
one. This theory was testable and Lorentz proudly submitted it to the
verdict of experiment.* Michelson, jointly with Morley, took up the
challenge. The relative velocity of the earth to the ether again seemed to
be zero, in conflict with Lorentz’s theory. By this time, Michelson had
become more cautious in interpreting his data and even thought of the
possibility that the solar system as a whole might have moved in the
opposite direction tothe earth; therefore he decided to repeat the experiment
1 This transpires, obliquely, from the concluding section of his [1881].

2 Michelson [1881], p. 128. My italics. % Michelson and Morley [1887], p. 335.
4 Lorentz [1886]. For the inconsistency of Stokes’s theory also cf. his [18925],

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 161

‘at intervals of three months and thus avoid all uncertainty’.! Michelson,
in his second paper, does not talk any more about ‘necessary conclusions’
and ‘direct contradictions’. He only thinks that from his experiment ‘it
appears, from all that precedes, reasonably certain that if there be any
relative motion between the earth and the luminiferous ether, it must be
small; quite small enough entirely to refute Fresnel’s explanation of
aberration’. Thus in this paper Michelson still claims to have refuted
Fresnel’s theory (and also Lorentz’s new theory); but there is not a word
about his old 1881 claim that he refuted ‘the theory of stationary ether’ in
general. (Indeed, he believed that in order to do so, he would have to test
the ether wind also at high altitudes, ‘at the top of an isolated mountain
peak, for instance’.*)

While some ether-theorists—like Kelvin—did not trust Michelson’s
‘experimental skill’,4 Lorentz pointed out that, in spite of Michelson’s
naive claim, even his new experiment ‘furnishes no evidence for the ques-
tion for which it was undertaken’.® One can regard Fresnel’s theory per-
fectly well as an interpretative theory, which interprets facts, rather than is
refutable by them, and then, Lorentz showed, ‘the significance of the
Michelson—Morley experiment lies rather in the fact that it can teach us
something about the changes in the dimensions’®: the dimensions of bodies
is affected by their movement through the ether. Lorentz elaborated this
‘creative shift’ within Fresnel’s programme with great ingenuity and
thereby claimed to have ‘removed the contradiction between Fresnel’s
theory and Michelson’s result’.? But he admitted that ‘since the nature of
the molecular forces is entirely unknown to us, it is impossible to test the
hypothesis’®: at least for the time being it could predict no novel facts.®

1 Michelson and Morley [1887], p. 341. But Pearce Williams points out that he never did.
(Pearce Williams [1968], p. 34.) 2 Ibid. p. 341. My italics.

3 Michelson and Morley [1887]. This remark shows that Michelson realized that his
1887 experiment was completely consistent with an ether wind higher up. Max Born, in
his [1920], that is, thirty-three years later, asserted that from the 1887 experiment ‘we must
conclude that the ether wind does not exist’. (My italics).

4 Kelvin said in the 1900 International Congress of Physics that ‘the only cloud in the
clear sky of the [ether] theory was the null result of the Michelson—Morley experiment’
(cf. Miller [1925]) and immediately persuaded Morley and Miller, who were there, to
repeat the experiment.

5 Lorentz [1892a]. 5 Ibid. My italics.

7 Lorentz [1895]. 8 Lorentz [18925].

® Fitzgerald at the same time, independently of Lorentz, produced a testable version of
this ‘creative shift’ which was quickly refuted by ‘Trouton’s, Rayleigh’s and Brace’s experi-
ments: it was theoretically but not empirically progressive. Cf. Whittaker [1947], p. 53
and Whittaker [1953], pp. 28—30.

There is a widespread view that Fitzgerald’s theory was ad hoc. What contemporary

physicists meant was that the theory was ad hoc, (cf. above, p. 125, footnote 1): that there
was ‘no independent [positive] evidence’ for it. (Cf. e.g. Larmor [1904], p. 624.) Later,

162 IMRE LAKATOS

In the meanwhile, in 1897, Michelson carried out his long planned
experiment to measure the velocity of ether wind on mountain tops. He
found none. Since he had thought earlier that he had proved Stokes’s
theory which predicted an ether wind higher up, he was dumbfounded. If
Stokes’s theory was still correct, the gradient of the velocity of the ether
had to be very small. Michelson had to conclude that ‘the earth’s influence
upon the ether extended to distances of the order of the earth’s diameter’.}
He thought that this was an ‘improbable’ result, and decided that in 1887 he
had drawn the wrong conclusion from his experiment: it was Stokes’s theory
which had to be rejected and Fresnel’s which had to be accepted; and he
decided that he would accept any reasonable auxiliary hypothesis to have it
saved, including Lorentz’s 1892 theory.2, He now seemed to prefer the
Fitzgerald—Lorentz contraction and by 1904 his colleagues at Case were
trying to find out whether this contraction varies with different materials.?

While most physicists tried to interpret Michelson’s experiments within
the framework of the ether programme, Einstein, unaware of Michelson,
Fitzgerald and Lorentz, but stimulated primarily by Mach’s criticism of
Newtonian mechanics, arrived at a new, progressive research programme.
This new programme not only ‘predicted’ and explained the outcome of
the Michelson—Morley experiment but also predicted a huge array of
previously undreamt-of facts, which obtained dramatic corroborations. It
was only then, twenty-five years later, that the Michelson—Morley experi-
ment came to be seen as ‘the greatest negative experiment in the history of
science’.5 But this could not be seen instantly. Even if the experiment was
negative, it was not clear, negative exactly to what? Moreover, Michelson
in 1881 thought that it was also positive: he held that he had refuted Fresnel’s

under Popper’s influence the term ‘ad hoc’ was primarily used in the sense of ad hoc,, that
there was no independent test possible for it. But, as the refuting experiments show, it is a
mistake to claim, as Popper does, that Fitzgerald’s theory was ad hoc, (cf. Popper [1934],
section 20). This shows again how important it is to separate ad hoc,, and ad hoc.

When Griinbaum, in his [1959a], pointed out Popper’s mistake, Popper admitted it but
replied that Fitzgerald’s theory was certainly more ad hoc than Einstein’s (Popper [1959}]),
and that this provides yet another ‘. . . excellent example of “degrees of ad-hocness”” and
of one of the main theses of [his] book—that degrees of ad-hocness are related (inversely) to
degrees of testability and significance’. But the difference is not simply a matter of degrees
of a unique ad-hocness which can be measured by testability. Also cf. below, p. 175.

1 Michelson [1897], p. 478.

2 Lorentz, indeed, immediately commented : ‘While [Michelson] considers so far-reaching
an influence of the earth improbable, I should, on the contrary, expect it’ (Lorentz [1897];
my italics). 3 Morley and Miller [1904].

4 There has been a considerable controversy about the historico-heuristic background
of Einstein’s theory, in the light of which this statement may turn out to be false,

5 Bernal [1965], p. 530. For Kelvin, in 1905, it was only a ‘cloud in the clear sky’: cf.
above, p. 161, footnote 4.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 163

but had verified Stokes’s theory. Michelson himself and then Fitzgerald
and Lorentz explained the result also positively within the ether pro-
gramme.! As it is with all experimental results, its negativity for the old
programme was established only later, by the slow accumulation of ad hoc
attempts to account for it within the degenerating old programme and by
the gradual establishment of a new progressive victorious programme in
which it has become a positive instance. But the possibility of the rehabili-
tation of some part of the ‘degenerating’ old programme could never be
rationally excluded.

Only an extremely difficult and—indefinitely—long process can establish
a research programme as superseding its rival; and it is unwise to use the
term ‘crucial experiment’ too rashly. Even when a research programme is
seen to be swept away by its predecessor, it is not swept away by some
‘crucial’ experiment; and even if some such crucial experiment is later
called in doubt, the new research programme cannot be stopped without a
powerful progressive upsurge of the old programme.? The negativity—and
importance—of the Michelson—Morley experiment lies primarily in the
progressive shift in the mew research programme to which it came to lend
powerful support, and its ‘greatness’ is only a reflection of the greatness of
the two programmes involved.

It would be interesting to give a detailed analysis of the rival shifts
involved in the waning fortunes of the ether theory. But under the influence
of naive falsificationism the most interesting degenerating phase in the
ether theory after Michelson’s ‘crucial experiment’ is simply ignored by
most Einsteinians. They believe that the Michelson—Morley experiment
single-handedly defeated the ether theory, the tenacity of which was only
due to obscurantist conservatism. On the other hand, this post-Michelson
period of the ether theory is not scrutinized critically by the anti-Einstein-
ians, who believe that the ether theory suffered no setback whatsoever:
what is good in Einstein’s theory was essentially in Lorentz’s ether theory
and Einstein’s victory is only due to positivist fashion. But, in fact, Michel-
son’s long series of experiments from 1881 to 1935, conducted in order to
test subsequent versions of the ether programme provides a fascinating

1 Indeed, Chwolson’s excellent physics textbook said in 1902 that the probability of the
ether hypothesis borders on certainty. (Cf. Einstein [1909], p. 817.)

2 Polanyi tells us with gusto how, in 1925, in his presidential address to the American
Physical Society, Miller announced that Michelson’s and Morley’s reports notwithstanding,
he had ‘overwhelming evidence’ for an ether-drift; yet the audience remained committed
to Einstein’s theory. Polanyi draws the conclusion that no ‘ “objectivist” framework’ can
account for the scientist’s acceptance or rejection of theories (Polanyi [1958], pp. 12-14).
But my reconstruction makes the tenacity of the Einsteinian research programme in the

face of alleged contrary evidence a completely rational phenomenon and thereby undermines
Polanyi’s ‘post-critical’-mystical message.

164 IMRE LAKATOS

example of a degenerating problemshift.! (But problemshifts may get out
of degenerating troughs. It is well known that Lorentz’s ether theory can
easily be strengthened in such a way that it becomes, in an interesting
sense, equivalent with Einstein’s no-ether theory.2 The ether may, in the
context of a major ‘creative shift’, still return.*)

The fact that we heed hindsight to evaluate experiments explains why,
between 1881 and 1886, Michelson’s experiment was not even mentioned
in the literature. Indeed, when a French physicist, Potier, pointed out to
Michelson his 1881 mistake, Michelson decided not to publish a correc-
tion note. He explains the reason for this decision in a letter to Rayleigh in
March 1887: ‘I have repeatedly tried to interest my scientific friends in
this experiment without avail, and the reason for my never publishing the
correction (I am ashamed to confess it) was that I was discouraged at the
slight attention the work received, and did not think it worthwhile.”* This
letter, incidentally, was a reply to a letter from Rayleigh which drew
Michelson’s attention to Lorentz’s paper. This letter triggered off the
1887 experiment. But even after 1887, and even after 1905, the Michelson-
Morley experiment was not yet generally regarded as disproving the exis-
tence of the ether, and with good reason. This may explain why Michelson
was awarded his Nobel Prize (in 1907), not for ‘refuting the ether theory’,
but ‘for his optical precision instruments and the spectro-scopic and method-
ological investigations carried out with their aid’; and why the Michelson—
Morley experiment was not even mentioned in the presentation speeches.
Michelson, in his Nobel Lecture, did not mention it; and he kept quiet

1 One typical sign of the degeneration of a programme which is not discussed in this paper
is the proliferation of contradictory ‘facts’. Using a false theory as an interpretative theory,
one may get—without committing any ‘experimental mistake’—contradictory factual proposi-
tions, inconsistent experimental results. Michelson, who stuck to the ether to the bitter end,
was primarily frustrated by the inconsistency of the ‘facts’ he arrived at by his ultra-precise
measurements. His 1887 experiment ‘showed’ that there was no ether wind on the earth’s
surface. But aberration ‘showed’ that there was. Moreover, his own 1925 experiment
(either never mentioned or, as in Jaffé’s [1960], misrepresented) also ‘proved’ that there
was one (cf. Michelson and Gale [1925] and, for a sharp criticism, Runge [1925]).

2 Cf. e.g. Ehrenfest [1913], pp. 17-18, quoted and discussed by Dorling in his [1968].
But one should not forget that two specific theories, while being mathematically (and observa-
tionally) equivalent, may still be embedded into different rival research programmes, and the
power of the positive heuristic of these programmes may well be different. This point has been
overlooked by proposers of such equivalence proofs (a good example is the equivalence
proof between Schrédinger’s and Heisenberg’s approach to quantum physics). Also cf.
above, p. 1§5, footnote 2.

3Cf eg. Dirac [1951]: ‘If one reexamines the question in the light of present-day
knowledge, one finds that the aether is no longer ruled out by relativity, and good reasons
can now be advanced for postulating an aether.’ Also cf. the concluding paragraph of
Rabi [1961] and Prokhovnik [1967].

4 Shankland [1964], p. 29.

5 My italics.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 165

about the fact that although he might have originally devised his instru-
ments to measure precisely the velocity of light, he was compelled to
improve them for testing some specific ether theories and that the ‘pre-
cision’ of his 1887 experiment was largely motivated by Lorentz’s theoret-
ical criticism: a fact which standard contemporary literature never
mentions.}

Finally, one tends to forget that even if the Michelson—Morley experi-
ment had shown an ‘ether wind’, Einstein’s programme might have been
victorious nonetheless. When Miller, an ardent champion of the classical
ether programme, published his sensational claim that the Michelson—
Morley experiment was sloppily conducted and in fact there was an ether
wind, the news correspondent of Science crowed that ‘Professor Miller’s re-
sults knock out the relativity theory radically’.? In Einstein’s view, however,
even if Miller had reported the true state of affairs ‘[only] the present form
of relativity theory’ would have to be abandoned.? In fact, Synge pointed
out that Miller’s results, even if taken at their face value, do not conflict
with Einstein’s theory: only Miller’s explanation of them does. One can
easily replace the extant auxiliary theory of rigid bodies by a new, Gardner—
Synge theory, and then Miller’s results are fully digested within Einstein’s
programme.*

(d2) The Lummer—Pringsheim experiments.

Let us discuss another alleged crucial experiment. Planck claimed that
Lummer’s and Pringsheim’s experiments, which ‘refuted’ Wien’s and
Rayleigh’s and Jeans’s laws of radiation at the turn of the century, ‘led to’"—
or ‘even brought about’—the quantum theory.® But again the role of
these experiments is much more complicated and is very much in line
with our approach. It is not simply that Lummer’s and Pringsheim’s ex-
periments put an end to the classical approach but were neatly explained
by quantum physics. On the one hand, some early versions of quantum
theory by Einstein entail Wien’s law and therefore were no less refuted by

1 Einstein himself tended to believe that Michelson devised his interferometer in order
to test Fresnel’s theory. (Cf. Einstein [1931].) Incidentally, Michelson’s early experiments
on spectrum lines—like his [1881-2]—-were also relevant to the ether theories of his day.
Michelson over-emphasized his success in ‘precise measurements’ only when he was
frustrated by his lack of success in evaluating their relevance for theories. Einstein, who
disliked precision for its own sake, asked him why he devoted so much energy to it. Michel-
son’s answer was ‘because he found it fun.’ (Cf. Einstein [1931].)

2 Science [1925].

3 Einstein [1927]. My italics,

4 Synge [1952-4].

5 Planck [1929]. Popper, in his [1934], section 30, Gamow in his [1966] (p. 37), take
over this locution. Of course, observation statements do not ‘lead’ to some uniquely deter-
mined theory.

166 IMRE LAKATOS

Lummer’s and Pringsheim’s experiments than the classical theory.1 On the
other hand, several classical explanations of the Planck formula were
offered. For instance, at the 1913 meeting of the British Association for the
Advancement of Science, there was a special meeting on radiation, attended
among others by Jeans, Rayleigh, J. J. Thomson, Larmor, Rutherford,
Bragg, Poynting, Lorentz, Pringsheim and Bohr. Pringsheim and Rayleigh
were studiedly neutral about quantum theoretical speculations, but Pro-
fessor Love ‘represented the older views, and maintained the possibility of
explaining facts about radiation without adopting the theory of quanta.
He criticized the application of the equi-partition of energy theory, on
which part of the quantum theory rests. The evidence for the quantum
theory of most weight is the agreement with experiment of Planck’s
formula for the emissivity of a black body. From the mathematical point
of view, there may be many more formulae which would agree equally
well with the experiments. A formula due to A. Korn was dealt with,
which gave results over a wide range, showing just about as good agree-
ment with experiment as the Planck formula. In further contention that
the resources of ordinary theory are not exhausted, he pointed out that it may
be possible to extend the calculation for the emissivity of a thin plate due
to Lorentz to other cases. For this calculation no simple analytical ex-
pression represents the results over the whole range of wavelengths, and
it may well be that in the general case no simple formula exists which is
applicable to all wavelengths. Planck’s formula may, in fact, be nothing
more than an empirical formula.’ One example of classical explanations
was due to Callendar: “The disagreement with experiment of Wien’s well-
known formula for the partition of energy in full radiation, is readily
explained if we assume that it represents only the intrinsic energy. ‘The
corresponding value of the pressure is very easily deduced by reference to
Carnot’s principle, as Lord Rayleigh has indicated. The formula which I
have proposed (Phil. Mag., October 1913) is simply the sum of the pressure
and energy-density thus obtained, and gives very satisfactory agreement
with experiment, both for radiation and specific heat. I prefer it to Planck’s
formula (among other reasons) on the ground that the latter cannot be
reconciled with the classical thermodynamics, and involves the conception
of a quantum, or indivisible unit of action, which is unthinkable. The
corresponding physical magnitude on my theory, which I have elsewhere
called a molecule of caloric, is not necessarily indivisible, but bears a
very simple relation to the intrinsic energy of an atom, which is all that is

1 Cf, Ter Haar [1967], p. 18. A budding research programme usually starts by explaining
already refuted ‘empirical laws’—and this, in the light of my approach, may be rationally
regarded as a success. 2 Nature [1913-14], p- 306; my italics.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 167

required to explain the facts that radiation may in special cases be emitted
in atomic units which are multiples of a particular magnitude.”

These quotations may have been tediously long but at least they show
again convincingly the absence of instant crucial experiments. Lummer’s
and Pringsheim’s refutations did not eliminate the classical approach to the
radiation problem. The situation can be better described by pointing out
that Planck’s original ‘ad hoc’ formula*—which fitted (and corrected)
Lummer’s and Pringsheim’s data—could be explained progressively
within the new quantum theoretical programme,’ while neither his ‘ad
hoc’ formula, nor its ‘semi-empirical’ rivals could be explained within the
classical programme except at the price of a degenerating problemshift.
The ‘progressive’ development, incidentally, hinged on a ‘creative shift’:
the replacement (by Einstein) of the Boltzman—Maxwell by the Bose-
Einstein statistics,4 The progressiveness of the new development was
abundantly clear: in Planck’s version it predicted correctly the value of the
Boltzman-—Planck constant and in Einstein’s version it predicted a stunning
series of further novel facts.5 But before the invention of the new—but
sadly ad hoc—auxiliary hypotheses in the old programme, before the un-
folding of the new programme, and before the discovery of the new facts
indicating a progressive problemshift in the latter, the objective relevance
of the Lummer-Pringsheim experiments was very limited.

4 Callendar [1914].

2 | am referring to Planck’s formula as given in his [1900a@] in which he admitted that
after having tried for a long time to prove that ‘Wien’s law must be necessarily true’, the
‘law’ was refuted. So he switched from proving lofty eternal jaws to ‘constructing com-
pletely arbitrary expressions’. But of course any physical theory turns out to be ‘completely
arbitrary’ by justificationist standards. In fact, Planck’s arbitrary formula contradicted—
and victoriously corrected—contemporary empirical evidence. (Planck told this part of the
story in his scientific autobiography.) Of course, in an important sense, Planck’s originai
radiation formula was ‘arbitrary’, ‘formal’, ‘ad hoc’: it was a rather isolated formula which
was not part of a research programme. (Cf. below, p. 175, footnote 3.) As he himself put it:
‘Even if the absolutely precise validity of the radiation formula is taken for granted, so long
as it had merely the standing of a law disclosed by a lucky intuition, it could not be expected
to possess more than a formal significance. For this reason, on the very day when I formulated
this law, I began to devote myself to the task of investing it with a true physical meaning’
({1947], p. 41). But the primary importance of ‘investing the formula with a physical mean-
ing’—not necessarily ‘true physical meaning’—is that such interpretation frequently leads
to a suggestive research programme and growth.

3 First by Planck himself, in his [1900b] which ‘founded’ the research programme oj
quantum theory.

* This had already been done by Planck, but only inadvertently, as it were by mistake.
Cf. Ter Haar [1967], p. 18. Indeed, one role of Pringsheim’s and Lummer’s results was
to stimulate the critical analysis of the informal deductions in the quantum theory oi
radiation, deductions which were loaded with vital ‘hidden lemmas’ articulated only in the
later development. A most important step in this ‘articulating process’ was Ehrenfest’s
[1911]. 2 ® Cf. e.g. Joffé’s 1910 list (Joffé [1911], p. 547).

168 IMRE LAKATOS

(d 3) Beta-decay versus conservation laws.

Finally, I shall tell a story of an experiment which very nearly, but not
quite, became ‘the greatest negative experiment in the history of science’.
The story again illustrates the supreme difficulties of deciding exactly what
one learns from experience, what it ‘proves’ and what it ‘disproves’. ‘The
piece of experience under scrutiny will be Chadwick’s ‘observation’ of
beta decay in 1914. The story shows how an experiment may first be re-
garded as presenting a routine puzzle within a research programme, then
nearly promoted to the rank of ‘crucial experiment’, and then again down-
graded to presenting a (new) routine puzzle, all this depending on the whole
changing theoretical and empirical landscape. Most conventional accounts
are confused by these changes and prefer to falsify history.

When Chadwick discovered the continuous spectrum of radioactive
beta-emission in 1914, nobody thought that this curious phenomenon had
anything to do with conservation laws. T'wo ingenious rival explanations
were offered in 1922, both within the framework of the atomic physics of
the day, one by L. Meitner, the other by C. D. Ellis. According to Miss
Meitner, the electrons were partly primary electrons from the nucleus,
partly secondary electrons from the electron shell. According to Mr Ellis,
they were all primary electrons. Both theories contained sophisticated
auxiliary hypotheses, but both predicted novel facts. The predicted facts
contradicted each other and the experimental testimony supported Ellis
against Meitner.? Miss Meitner appealed; the experimental ‘appeal court’
refused to support her, but ruled that one crucial auxiliary hypothesis in
Ellis’s theory had to be rejected.? The result of the contest was a draw.

Still nobody would have thought that Chadwick’s experiment defied the
law of conservation of energy, had not Bohr and Kramers arrived exactly
at the time of the Ellis-Meitner controversy at the idea that a consistent
theory could be developed only if they renounced the principle of con-
servation of energy in single processes. One of the main features of the
fascinating Bohr-Kramers-Slater theory in 1924 was that the classical
laws of conservation of energy and momentum were replaced by statis-
tical ones.* This theory (or, rather, ‘programme’) was immediately ‘refuted’

1A notable partial exception is Pauli’s account (Pauli [1958]). In what follows I am
trying both to correct Pauli’s story and to show that its rationality can be easily seen in the
light of our approach.

? Ellis and Wooster [1927].

3 Meitner and Orthmann [1939].

4 Slater co-operated only reluctantly in sacrificing the conservation principle. He
wrote to van der Waerden in 1964: ‘As you suspected, the idea of statistical conservation
of energy and momentum was put into the theory by Bohr and Kramers, quite against
my better judgment.’ Van der Waerden does his amusing best to exonerate Slater from the
terrible crime of being responsible for a false theory (van der Waerden [1967], p. 13).

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 169

and none of its consequences corroborated ; indeed, it was never sufficiently
developed to explain beta-decay. But in spite of the immediate abandon-
ment of this programme (not simply because of its ‘refutations’ by the
Compton-Simon and Bothe-Geiger experiments but because of the emer-
gence of a powerful rival: the Heisenberg-Schrédinger programme’),
Bohr remained convinced that the non-statistical conservation laws would
finally have to be abandoned and that the beta-decay anomaly would
never be explained until these laws were replaced; at which time beta-
decay would be seen as a crucial experiment against the conservation laws.
Gamow tells us how Bohr tried to use the idea of non-conservation of
energy in beta-decay for an ingenious explanation of the seemingly eternal
production of energy in stars. Only Pauli, in his Mephistophelian
urge to defy the Lord, remained conservative® and devised, in 1930, his
neutrino theory in order to explain beta decay and in order to save the
principle of conservation of energy. He communicated his idea in a jocular
letter to a conference in Tiibingen—he himself preferred to stay in Ziirich
to attend a ball.* He first mentioned it in a public lecture in 1931 in Pasa-
dena, but he did not allow the lecture to be published because he felt
‘unsure’ about it. Bohr, at that time (in 1932), still thought that—at least
in nuclear physics—one may have ‘to renounce the very idea of energy
balance’.’ Pauli finally decided to publish his talk on the neutrino which he
delivered to the 1933 Solvay conference, in spite of the fact that ‘the
reception at the Congress, except for two young physicists, was sceptical’.®
But Pauli’s theory had some methodological merits. It saved not only the
principle of conservation of energy but also the principle of conservation of
spin and statistics: it explained not only the beta-decay spectrum but, at
the same time, the ‘nitrogen anomaly’.? By Whewellian standards this
‘consilience of inductions’ should have been sufficient to establish the

‘ Popper is wrong to suggest that these ‘refutations’ were sufficient to bring about the
downfall of this theory. (Popper [1963], p. 242.)

2 Gamow [1966], pp. 72-4. Bohr never published this theory (it was untestable as it
stood) but ‘it looked’—writes Gamow—‘as if he would not be greatly surprised if it were
true’, Gamow does not date this unpublished theory but it seems that Bohr entertained it
in 1928-9 when Gamow was working in Copenhagen.

3 Cf. the amusing play ‘Faust’ produced in Bohr’s institute in 1932; published by Gamow
as an appendix to his [1966].

4 Cf. Pauli [1958], p. 160.

® Bohr [1932]. Ehrenfest too sided firmly with Bohr against the neutrino. Chadwick’s
discovery of the neutron in 1932 only slightly shook their opposition: they still dreaded
the idea of a particle which has neither charge nor, possibly, even (rest) mass, but only
‘disembodied’ spin. 6 Wu [1966].

7 For a fascinating discussion of the open problems presented by the beta-decay and by
the nitrogen anomaly, cf. Bohr’s Faraday Lecture in 1930, read before, but published after,
Pauli’s solution (Bohr [1930], especially pp. 380-3).

170 IMRE LAKATOS

respectability of Pauli’s theory. But on our criteria, the successful predic-
tion of some novel fact was needed. This too was provided by Pauli’s
theory. For Pauli’s theory had an interesting observable consequence: if it
was right, the B-spectra had to have a clear upper bound. This question
was at the time undecided, but Ellis and Mott became interested! and soon,
Ellis’s student, Henderson, showed that the experiments supported Pauli’s
programme.? Bohr was not impressed. He knew that if a major programme
based on statistical conservation of energy ever got going, the growing belt
of auxiliary hypotheses would take proper care of the most negative-
looking evidence.

Indeed, in these years most leading physicists thought that in nuclear
physics the laws of conservation of energy and momentum break down.®
The reason was stated clearly by Lise Meitner who admitted defeat only in
1933: ‘All the attempts to uphold the validity of the law of conservation of
energy also for single processes demanded a second process [in the beta-
decay]. But no such process was found . . .“: that is, the conservation pro-
gramme for the nucleus showed an empirically degenerating problemshift.
There were several ingenious attempts to account for the continuous beta-
emission spectrum without assuming a ‘thief particle’.5 These attempts
were discussed with great interest,® but they were abandoned because they
failed to establish a progressive shift.

At this point, Fermi entered on the scene. In 1933-4 he reinterpreted
the beta-emission problem in the framework of the research programme of
the new quantum theory. Thus he initiated a small new research pro-
gramme of the neutrino (which later grew into the programme of weak
interactions). He calculated some first crude models.’ Although his theory
did not yet predict any new fact, he made it clear that this was only a
matter of some further work.

Two years passed and Fermi’s promise was still not fulfilled. But the
new programme of quantum physics developed fast, at least as far as the
non-nuclear phenomena were concerned. Bohr became convinced that
some of the basic original ideas of the Bohr-Kramers-Slater programme
were now firmly embedded in the new quantum programme and that the

1 Ellis and Mott [1933].

# Henderson [1934].

3 Mott [1933], p. 823. Heisenberg, in his celebrated [1932], in which he introduced the
proton-neutron model of the nucleus, pointed out that ‘because of the breakdown of the
conservation of energy in the beta-decay one cannot give a unique definition of the binding
energy of the electron within the neutron’ (p. 164).

4 Meitner [1933], Pp. 132.

5 E.g. Thomson [1929] and Kudar [1929-30].

6 For a most interesting discussion cf. Rutherford, Chadwick and Ellis [1930], pp. 335-6.

7 Fermi [1933] and [1934]. ae

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES iI7I

new programme solved the intrinsic theoretical problems of the old
quantum programme without touching the conservation laws. Therefore
Bohr followed Fermi’s work with sympathy, and in 1936, in an unusual
sequence of events, gave it, by our standards prematurely, public support.

In 1936 Shankland devised a new test of rival theories of photon scatter-
ing. His results seemed to support the discarded Bohr—Kramers-Slater
theory and undermine the reliability of experiments which, more than a
decade earlier, refuted it.1 Shankland’s paper created a sensation. Those
physicists who abhorred the new trend were quick to hail Shankland’s
experiment. Dirac, for instance, immediately welcomed back the ‘refuted’
Bohr—Kramers-Slater programme, wrote a very sharp article against the
‘so-called quantum electrodynamics’ and demanded ‘a profound altera-
tion in current theoretical ideas, involving a departure from the conserva-
tion laws [in order] to get a satisfactory relativistic quantum mechanics’?
In the article Dirac suggested again that beta-decay may well turn out to
be a piece of crucial evidence against the conservation laws and made fun
of the ‘new unobservable particle, the neutrino, specially postulated by
some investigators in an attempt formally to preserve conservation of
energy by assuming the unobservable particle to carry off the balance’.®
Immediately afterwards Peierls joined the discussion. Peierls suggested that
Shankland’s experiment may turn out to refute even the statistical conser-
vation of energy. He added: “That, too, seems satisfactory, once detailed
conservation has been abandoned.”4

In Bohr’s Copenhagen institute, Shankland’s experiments were immed-
iately repeated and discarded. Jacobsen, a colleague of Bohr reported this
in a letter to Nature. Jacobsen’s results were accompanied by a letter from
Bohr himself, who firmly came out against the rebels, and in defence of
Heisenberg’s new quantum programme. In particular, he came out in
defence of the neutrino against Dirac: ‘It may be remarked that the
grounds for serious doubts as regards the strict validity of the conserva-
tion laws in the problem of the emission of B-rays from atomic nuclei are
now largely removed by the suggestive agreement between the rapidly
increasing experimental evidence regarding B-ray phenomena and the
consequences of the neutrino hypotheses of Pauli so remarkably de-
veloped in Fermi’s theory.’®

Fermi’s theory, in its first versions, had no striking empirical success.
Indeed, even the available data, especially in the case of RaE, on which
beta emission research then centred, sharply contradicted Fermi’s 1933-4
theory. He wanted to deal with these in the second part of his paper which,

1 Shankland [1936]. ? Dirac [1936]. * Dirac [1936].
4 Peierls [1936]. 5 Bohr [1936].

172 IMRE LAKATOS

however, was never published. Even if one construes Fermi’s 1933-4
theory as a first version of a flexible programme, by 1936 one could not
possibly detect any serious sign of a progressive shift. But Bohr wanted to
put his authority behind Fermi’s daring application of Heisenberg’s new
big programme to the nucleus; and since Shankland’s experiment and
Dirac’s and Peierls’s attack brought the beta-decay into the focus of the
criticism of the new big programme, he over-praised Fermi’s neutrino
programme which promised to fill in a sensitive gap. No doubt, the later
development spared Bohr from a dramatic humilation: the programmes
based on conservation principles progressed, while no progress was made
in the rival camp.”

The moral of this story is again that the status of an experiment as
‘crucial’ depends on the status of the theoretical competition in which it is
embedded. As the fortunes of the competing camps wax or wane, the
interpretation and appraisal of the experiment may change.

Our scientific folklore however is impregnated with theories of instant
rationality, The story which I described is falsified in most accounts and
reconstructed in terms of some wrong theory of rationality. Even the very
best popular expositions teem with such falsifications. Let me mention
two examples.

In one paper we learn this about beta-decay: ‘When this situation was
faced for the first time, the alternatives seemed grim. Physicists either had
to accept a breakdown of the law of energy conservation, or they had to
suppose the existence of a new and unseen particle. Such a particle, emitted
along with the proton and the electron in the disintegration of the neutron,
could save the central pillar of physics by carrying off the missing energy.
This was in the early 1930s, when the introduction of a new particle was

1 Several physicists between 1933 and 1936 offered alternatives or proposed ad hoc
changes of Fermi’s theory; cf. e.g. Becke and Sitte [1933], Bethe and Peierls [1934], Kono-
pinski and Uhlenbeck [1934]. Wu and Moszkowski write in 1966 that ‘the Fermi theory
[i.e. programme] of B-decay is now known to predict with remarkable accuracy both the
relation between the rate of B-decay and the energy of disintegration, and also the shape of
B-spectra’. But they stress that ‘at the very beginning the Fermi theory unfortunately
met an unfair test. Until the time when artificial radioactive nuclei could be copiously
produced, RaE was the only candidate that beautifully fulfilled many experimental require-
ments as a f source for the investigation of its spectrum shape. How could we have known
then that the 8 spectrum of RaE would turn out to be only a very special case, one whose
spectrum has, in fact, been understood only very recently. Its peculiar energy dependence
defied what was expected of the simple Fermi theory of # decay and greatly slackened the
pace of the theory’s [i.e. programme’s] initial progress’ (Wu and Moszkowski [1966], p. 6).

* It is very doubtful whether Fermi’s neutrino programme was progressive or degenerating
even between 1936 and 1950; and after 1950 the verdict is still not crystal clear. But this I
shall try to discuss in some other occasion. (Incidentally, Schrédinger stood up for the

statistical interpretation of the conservation principles in spite of his crucial role in the
development of new quantum physics; cf. his [1958].)

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 173

not the casual matter it is today. Nevertheless, after only the briefest
vacillation, physicists chose the second alternative.’! Of course, even the
discussed alternatives were many more than two and the ‘vacillation’ was
certainly not ‘the briefest’.

In a well-known textbook of philosophy of science we learn that (1) ‘the
law (or principle) of the conservation of energy was seriously challenged by
experiments on beta-ray decay whose outcome could not be denied’; that
(2) ‘nevertheless, the law was not abandoned, and the existence of a new
kind of entity (called a “neutrino”) was assumed in order to bring the law
into concordance with experimental data’; and that (3) ‘the rationale for
this assumption is that the rejection of the conservation law would deprive
a large part of our physical knowledge of its systematic coherence’.? But all
the three points are wrong. (1) is wrong because no law can be ‘seriously
challenged’ by experiments only; (2) is wrong because new scientific hypo-
theses are assumed not simply in order to patch up gaps between data and
theory but in order to predict novel facts; and (3) is wrong because at the
time it seemed that only the rejection of the conservation law would secure
the ‘systematic coherence’ of our physical knowledge.

(d 4) Conclusion. The requirement of continuous growth.

There are no such things as crucial experiments, at least not if these are
meant to be experiments which can instantly overthrow a research pro-
gramme. In fact, when one research programme suffers defeat and is super-
seded by another one, we may—with long hindsight—call an experiment
crucial if it turns out to have provided a spectacular corroborating instance
for the victorious programme and a failure for the defeated one (in the sense
that it was never ‘explained progressively’—or, briefly, ‘explained’’—within
the defeated programme). But scientists, of course, do not always judge heur-
istic situations correctly. A rash scientist may claim that his experiment de-
feated a programme, and parts of the scientific community may even, rashly,
accept his claim. But if a scientist in the ‘defeated’ camp puts forward a
few years later a scientific explanation of the allegedly ‘crucial experiment’
within (or consistent with) the allegedly defeated programme, the honorific
title may be withdrawn and the ‘crucial experiment’ may turn from a defeat
into a new victory for the programme.

Examples abound. There were many experiments in the eighteenth
century which were, as a matter of historico-sociological fact, widely
accepted as ‘crucial’ evidence against Galileo’s law of free fall, and Newton’s
theory of gravitation. In the nineteenth century there were several ‘crucial

1 Treiman [1959]; my italics. 2 Nagel [1961], pp. 65-6,

3 Cf. above, p. 119, footnote 1,

174 IMRE LAKATOS

experiments’ based on measurements of light velocity which ‘disproved’
the corpuscular theory and which turned out later to be erroneous in the
light of relativity theory. These ‘crucial experiments’ were later deleted
from the justificationist textbooks as manifestations of shameful short-
sightedness or even of envy. (Recently they reappeared in some new
textbooks, this time to illustrate the inescapable irrationality of scientific
fashions.) However, in those cases in which ostensibly ‘crucial experi-
ments’ were indeed later borne out by the defeat of the programme,
historians charged those who resisted them with stupidity, jealousy, or
unjustified adulation of the father of the research programme in question.
(Fashionable ‘sociologists of knowledge’—or ‘psychologists of knowledge’—
tend to explain positions in purely social or psychological terms when, as a
matter of fact, they are determined by rationality principles. A typical
example is the explanation of Einstein’s opposition to Bohr’s comple-
mentarity principle on the ground that ‘in 1926 Einstein was forty-seven
years old. Forty-seven may be the prime of life, but not for physicists’.)

In the light of this paper, the utopian idea of instant rationality becomes
a hallmark of most brands of epistemology. Justificationists wanted scien-
tific theories to be proved even before they were published; probabilists
hoped a machine could flash up instantly the value (degree of confirma-
tion) of a theory, given the evidence; naive falsificationists hoped that
elimination at least was the instant result of the verdict of experiment.? I
hope I have shown that all these theories of instant rationality—and instant
learning—fail. The case studies of this section show that rationality works
much slower than most people tend to think, and, even then, fallibly.
Minerva’s owl flies at dusk. I also hope I have shown that the con-
tinuity in science, the tenacity of some theories, the rationality of a certain

1 Bernstein [1961], p. 129. In order to appraise progressive and degenerating elements
in rival problemshifts one must understand the ideas involved. But the sociology of know-
ledge frequently serves as a successful cover for illiteracy: most sociologists of knowledge do
not understand—or even care for—the ideas ; they watch the socio-psychological patterns
of behaviour. Popper used to tell a story about a ‘social psychologist’, Dr. X, studying
scientists’ group behaviour. He went into a physics seminar to study the psychology of
science. He observed the ‘emergence of a leader’, the ‘rallying round effect’ in some and
the ‘defence-reaction’ in others, the correlation between age, sex and aggressive behaviour,
etc. (Dr. X claimed to have used some sophisticated small-sample techniques of modern
statistics.) At the end of the enthusiastic account Popper asked Dr. X: “What was the
problem the group was discussing?’ Dr. X was surprised: ‘Why do you ask? I did not listen
to the words! Anyway, what has that to do with the psychology of knowledge?’

2 Of course, naive falsificationists may take some time to reach the ‘verdict of experiment’:
the experiment has to be repeated and critically considered. But once the discussion ends
up in an agreement among the experts, and thus a ‘basic statement’ becomes ‘accepted’,
and it has been decided which specific theory was hit by it, the naive falsificationist will
have little patience with those who still ‘prevaricate’.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 175

amount of dogmatism, can only be explained if we construe science as a
battleground of research programmes rather than of isolated theories. One
can understand very little of the growth of science when our paradigm of a
chunk of scientific knowledge is an isolated theory like ‘All swans are
white’, standing aloof, without being embedded in a major research pro-
gramme. My account implies a new criterion of demarcation between ‘mature
science’, consisting of research programmes, and ‘immature science’, consisting
of a mere patched up pattern of trial and error. For instance, we may have a
conjecture, have it refuted and then rescued by an auxiliary hypothesis
which is not ad hoc in the senses which we had earlier discussed. It may
predict novel facts some of which may even be corroborated.? Yet one may
achieve such ‘progress’ with a patched up, arbitrary series of disconnected
theories. Good scientists will not find such makeshift progress satisfactory ;
they may even reject it as not genuinely scientific. ‘They will call such
auxiliary hypotheses merely ‘formal’, ‘arbitrary’, ‘empirical’, ‘semi-
empirical’, or even ‘ad hoc’.3

Mature science consists of research programmes in which not only novel
facts but, in an important sense, also novel auxiliary theories, are anticipated;
mature science—unlike pedestrian trial-and-error—has ‘heuristic power’. Let
us remember that in the positive heuristic of a powerful programme there
is, right at the start, a general outline of how to build the protective belts:
this heuristic power generates the autonomy of theoretical science.4

This requirement of continuous growth is my rational reconstruction of the
widely acknowledged requirement of ‘unity’ or ‘beauty’ of science. It high-
lights the weakness of two—apparently very different—types of theorizing.
First, it shows up the weakness of programmes which, like Marxism or
Freudism, are, no doubt, ‘unified’, which give a major sketch of the sort of
auxiliary theories they are going to use in absorbing anomalies, but which

1 The elaboration of this demarcation in the two following paragraphs was improved
in the press, following invaluable discussions with Paul Meehl in Minneapolis in 1969.

? Earlier I distinguished, following Popper, two criteria of adhocness. I called ad hoc,
theories which had no excess content over their predecessors (or competitors) that is,
which did not predict any novel facts; I called ad hoc, theories which predicted novel
facts but completely failed: none of their excess content got corroborated (cf. above, p. 124,
footnote 3, and p. 125, footnote 1).

3 Planck’s radiation formula—given in his [1900a]—is a good example: cf. above, p. 167,
footnote 2. We may call such hypotheses which are not ad hoc,, not ad hoc,, but still un-
satisfactory in the sense specified in the text, ad hoc,. These three—unfailingly pejorative—
usages of ad hoc may provide a satisfactory entry in the Oxford English Dictionary.

It is intriguing to note that ‘empirical’ and ‘formal’ are both used as synonyms for our
ad hoc;.

Meehl, in his brilliant [1967], reports that in contemporary psychology—especially in
social psychology—many alleged ‘research programmes’ in fact consist of chains of such
ad hoc, stratagems. * Cf. above, p. 137

176 IMRE LAKATOS

unfailingly devise their actual auxiliary theories in the wake of facts with-
out, at the same time, anticipating others. (What novel fact has Marxism
predicted since, say, 1917?) Secondly, it hits patched-up, unimaginative
series of pedestrian ‘empirical’ adjustments which are so frequent, for inst-
ance, in modern social psychology. Such adjustments may, with the help of
so-called ‘statistical techniques’, make some ‘novel’ predictions and may
even conjure up some irrelevant grains of truth in them. But this theorizing
has no unifying idea, no heuristic power, no continuity. They do not add
up to a genuine research programme and are, on the whole, worthless.1

My account of scientific rationality, although based on Popper’s, leads
away from some of his general ideas. I endorse to some extent both Le
Roy’s conventionalism with regard to theories and Popper’s convention-
alism with regard to basic propositions. In this view scientists (and as I
have shown, mathematicians too*) are not irrational when they tend to
ignore counterexamples or as they prefer to call them, ‘recalcitrant’ or
‘residual’ instances, and follow the sequence of problems as prescribed by
the positive heuristic of their programme, and elaborate—and apply—
their theories regardless.? Contrary to Popper’s falsificationist moral-
ity, scientists frequently and rationally claim ‘that the experimental
results are not reliable, or that the discrepancies which are asserted to exist
between the experimental results and the theory are only apparent and

1 After reading Meehl [1967] and Lykken [1968] one wonders whether the function of
statistical techniques in the social sciences is not primarily to provide a machinery for
producing phoney corroborations and thereby a semblance of ‘scientific progress’ where,
in fact, there is nothing but an increase in pseudo-intellectual garbage. Meehl writes that
‘in the physical sciences, the usual result of an improvement in experimental design,
instrumentation, or numerical mass of data, is to increase the difficulty of the “observa-
tional hurdle” which the physical theory of interest must successfully surmount; whereas,
in psychology and some of the allied behaviour sciences, the usual effect of such improve-
ment in experimental precision is to provide an easier hurdle for the theory to surmount’.
Or, as Lykken put it: ‘Statistical significance [in psychology] is perhaps the least important
attribute of a good experiment; it is never a sufficient condition for claiming that a theory
has been usefully corroborated, that a meaningful empirical fact has. been established, or
that an experimental report ought to be published.’ It seems to me that most theorizing
condemned by Meehl and Lykken may be ad hoc;. Thus the methodology of research
programmes might help us in devising laws for stemming this intellectual pollution
which may destroy our cultural environment even earlier than industrial and traffic pollu-
tion destroys our physical environment. 2 Cf. my [1963-4].

3 Thus the methodological asymmetry between universal and singular statements vanishes.
We may adopt either by convention: in the ‘hard core’ we decide to ‘accept’ universal,
in the ‘empirical basis’ singular, statements. The logical asymmetry between universal
and singular statements is fatal only for the dogmatic inductivist who wants to learn only
from hard experience and logic. The conventionalist can, of course, ‘accept’ this logical
asymmetry: he does not have to be (although he may be) also an inductivist. He ‘accepts’
some universal statements, but not because he claims to deduce (or induce) them from
singular ones.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 177

that they will disappear with the advance of our understanding’.! When
doing so, they may not be ‘adopting the very reverse of that critical attitude
which ...is the proper one for the scientist’.2 Indeed, Popper is right in
stressing that ‘the dogmatic attitude of sticking to a theory as long as
possible is of considerable significance. Without it we could never find out
what is in a theory—we should give the theory up before we had a real
opportunity of finding out its strength; and in consequence no theory
would ever be able to play its role of bringing order into the world, of
preparing us for future events, of drawing our attention to events we should
otherwise never observe’.* Thus the ‘dogmatism’ of ‘normal science’ does
not prevent growth as long as we combine it with the Popperian recogni-
tion that there is good, progressive normal science and that there is bad,
degenerating normal science, and as long as we retain the determination to
eliminate, under certain objectively defined conditions, some research pro-
grammes.

The dogmatic attitude in science—which would explain its stable
periods—was described by Kuhn as a prime feature of ‘normal science’.4
But Kuhn’s conceptual framework for dealing with continuity in science is
socio-psychological: mine is normative. I look at continuity in science
through ‘Popperian spectacles’. Where Kuhn sees ‘paradigms’, I also
see rational ‘research programmes’.

4. THE POPPERIAN VERSUS THE KUHNIAN RESEARCH PROGRAMME

Let us now sum up the Kuhn-Popper controversy.

We have shown that Kuhn is right in objecting to naive falsificationism,
and also in stressing the continuity of scientific growth, the tenacity of some
scientific theories. But Kuhn is wrong in thinking that by discarding naive
falsificationism he has discarded thereby all brands of falsificationism.
Kuhn objects to the entire Popperian research programme, and he excludes
any possibility of a rational reconstruction of the growth of science. In a

1 Popper [1934], section 9. 2 Ibid.

3 Popper [1940], first footnote. We find a similar remark in his [1963], p. 49. But these
remarks are in prima facie contradiction with some of his remarks in [1934] (quoted above,
p. 111), and therefore may only be interpreted as signs of a growing awareness by Popper
of an undigested anomaly in his own research programme.

* Indeed, my demarcation criterion between mature and immature science can be
interpreted as a Popperian absorption of Kuhn’s idea of ‘normality’ as a hallmark of [mature]
science; and it also improved on our earlier argument against regarding such highly falsi-
fiable staternents as scientific. (Cf. above. p. 102.)

Incidentally, this demarcation between mature and immature seience appears already
in my [1961] and [1963-4], where I called the former ‘deductive guessing’ and the latter
‘naive trial and error’. (See e.g. [1963-4], section 7(c): ‘Deductive guessing versus naive
guessing.’)

178 IMRE LAKATOS

succint comparison of Hume, Carnap and Popper, Watkins points out that
the growth of science is inductive and irrational according to Hume, induc-
tive and rational according to Carnap, non-inductive and rational accord-
ing to Popper.1 But Watkins’s comparison can be extended by adding that
it is non-inductive and irrational according to Kuhn. In Kuhn’s view there
can be no logic, but only psychology of discovery.” For instance, in Kuhn’s
conception, anomalies, inconsistencies always abound in science, but in
‘normal’ periods the dominant paradigm secures a pattern of growth which
is eventually overthrown by a ‘crisis’. There is no particular rational cause
for the appearance of a Kuhnian ‘crisis’, ‘Crisis’ is a psychological concept ;
it is a contagious panic. Then a new ‘paradigm’ emerges, incommensurable
with its predecessor. There are no rational standards for their comparison.
Each paradigm contains its own standards. The crisis sweeps away not only
the old theories and rules but also the standards which made us respect
them. The new paradigm brings a totally new rationality. There are no
super-paradigmatic standards. The change is a bandwagon effect. Thus
in Kuhn’s view sctentific revolution is irrational, a matter for mob psychology.

The reduction of philosophy of science to psychology of science did not
start with Kuhn. An earlier wave of ‘psychologism’ followed the break~-
down of justificationism. For many, justificationism represented the only
possible form of rationality: the end of justificationism meant the end of
rationality. The collapse of the thesis that scientific theories are provable,
that the progress of science is cumulative, made justificationists panic. If
‘to discover is to prove’, but nothing is provable, then there can be no
discoveries, only discovery-claims. Thus disappointed justificationists—ex-
justificationists—thought that the elaboration of rational standards was a
hopeless enterprise and that all one can do is to study—and imitate—the
Scientific Mind, as it is exemplified in famous scientists. After the collapse
of Newtonian physics, Popper elaborated new, non-justificationist critical
standards. Now some of those who had already learned of the collapse of
justificationist rationality now learned, mostly by hearsay, of Popper’s
colourful slogans which suggested naive falsificationism. Finding them
untenable, they identified the collapse of naive falsificationism with the end
of rationality itself. The elaboration of rational standards was again regarded
as a hopeless enterprise; the best one can do is to study, they thought once
again, the Scientific Mind. Critical philosophy was to be replaced by what
Polanyi called a ‘post-critical’ philosophy. But the Kuhnian research

1 Watkins [1968], p. 281.

2 Kuhn [1965]. But this position is already implicit in his [1962].

3 Incidentally, just as some earlier ex-justificationists led the wave of sceptical irrational-
ism, so now some ex-falsificationists lead the new wave of sceptical irrationalism and
anarchism. This is best exemplified in Feyerabend [1970].

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 179

programme contains a new feature: we have to study not the mind of the
individual scientist but the mind of the Scientific Community. Individual
psychology is now replaced by social psychology; imitation of the great
scientists by submission to the collective wisdom of the community.

But Kuhn overlooked Popper’s sophisticated falsificationism and the
research programme he initiated. Popper replaced the central problem of
classical rationality, the old problem of foundations, with the new problem of
fallible-critical growth, and started to elaborate objective standards of this
growth. In this paper I have tried to develop his programme a step further.
I think this small development is sufficient to escape Kuhn’s strictures.

The reconstruction of scientific progress as proliferation of rival research
programmes and progressive and degenerative problemshifts gives a
picture of the scientific enterprise which is in many ways different from the
picture provided by its reconstruction as a succession of bold theories and
their dramatic overthrows. Its main aspects were developed from Popper’s
ideas and, in particular, from his ban on ‘conventionalist’, that is, content-
decreasing, stratagems. The main difference from Popper’s original ver-
sion is, I think, that in my conception criticism does not—and must not—
kill as fast as Popper imagined. Purely negative, destructive criticism, like
‘refutation’ or demonstration of an inconsistency does not eliminate a pro-
gramme. Criticism of a programme is a long and often frustrating process and
one must treat budding programmes leniently.? One may, of course, show up
the degeneration of a research programme, but it is only constructive
criticism which, with the help of rival research programmes, can achieve
real successes; and dramatic spectacular results become visible only with
hindsight and rational reconstruction.

Kuhn certainly showed that the psychology of science can reveal impor-
tant and, indeed, sad truths. But the psychology of science is not autono-
mous; for the—rationally reconstructed—growth of science takes place

1 Indeed, as I had already mentioned, my concept of a ‘research programme’ may be con-
strued as an objective, ‘third world’ reconstruction of Kuhn’s socio-psychological concept of
paradigm’: thus the Kuhnian ‘Gestalt-switch’ can be performed without removing one’s
Popperian spectacles.

(I have not dealt with Kuhn’s and Feyerabend’s claim that theories cannot be eliminated
on any objective grounds because of the ‘incommensurability’ of rival theories. Incom-
mensurable theories are neither inconsistent with each other, nor comparable for content.
But we can make them, by a dictionary, inconsistent and their content comparable. If we
want to eliminate a programme, we need some methodological determination. This deter-
mination is the heart of methodolegical falsificationism; for instance, no result of statistical
sampling is ever inconsistent with a statistical theory unless we make them inconsistent
with the help of Popperian rejection rules, cf. above, p. 109.)

? The reluctance of economists and other social scientists to accept Popper’s methodology

may have been partly due to the destructive effect of naive falsificationism on budding
research programmes.

180 IMRE LAKATOS

essentially in the world of ideas, in Plato’s and Popper’s ‘third world’, in the
world of articulated knowledge which is independent cf knowing sub-
jects.t Popper’s research programme aims at a description of this objective
scientific growth.? Kuhn’s research programme seems to aim at a description
of change in the (‘normal’) scientific mind (whether individual or com-
munal),? But the mirror-image of the third world in the mind of the indi-
vidual—even in the mind of the ‘normal’—scientists is usually a caricature
of the original; and to describe this caricature without relating it to the
third-world original might well result in a caricature of a caricature. One
cannot understand the history of science without taking into account the
interaction of the three worlds.

APPENDIX

POPPER, FALSIFICATIONISM AND THF ‘DUHEM-QUINE THESIS’

Popper began as a dogmatic falsificationist in the 1920s; but he soon
realized the untenability of this position and published nothing before he
invented methodological falsificationism. This was an entirely new idea in
the philosophy of science and it clearly originates with Popper, who put it
forward as a solution to the difficulties of dogmatic falsificationism. In-
deed, the conflict between the theses that science is both critical and

1 The first world is the material world, the second is the world of consciousness, the
third is the world of propositions, truth, standards: the world of objective knowledge. The
modern loci classici on this subject are Popper [1968a] and Popper [19688]; also, cf. Toulmin’s
impressive programme set out in his [1967]. It should be mentioned here that many pas-
sages of Popper [1934] and even of [1963] sound like descriptions of a psychological contrast
between the Critical Mind and the Inductivist Mind. But Popper’s psychologistic terms
can be, to a large extent, reinterpreted in third-world terms. Cf. Musgrave [1971].

2 In fact, Popper’s research programme extends beyond science. The concepts of ‘pro-
gressive’ and ‘degenerating’ problemshifts, the idea of proliferation of theories can be
generalized to any sort of rational discussion and thus serve as tools for a general theory of
criticism; cf. my [1970].

3 Actual state of minds, beliefs, etc., belong to the second world; states of the normal
mind belong to a limbo between the second and third. The study of actual scientific minds
belongs to psychology ; the study of the ‘normal’ (or ‘healthy’ etc.) mind belongs to a psycholo~
gistic philosophy of science. There are two kinds of psychologistic philosophies of science.
According to onekind there can be no philosophy of science: only a psychology of individual
scientists. According to the other kind there is a psychology of the ‘scientific’, ‘ideal’ or
‘normal’ mind: this turns philosophy of science into a psychology of this ideal mind and,
in addition, offers a psychotherapy for turning one’s mind into an ideal one. I discuss
this second kind of psychologism in detail in my [1970]. Kuhn does not seem to have noticed
this distinction.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 181

fallible is one of the central problems in Popperian philosophy. While
Popper offered a coherent formulation and criticism of dogmatic falsi-
ficationism, he never made a sharp distinction between naive and sophis-
ticated falsificationism. In an earlier paper,! I distinguished three Poppers:
Popper, Popper, and Popper,. Popper, is the dogmatic falsificationist who
never published a word: he was invented—and ‘criticized’—first by Ayer
and then by many others.? This paper will, I hope, finally kill this ghost.
Popper, is the naive falsificationist, Popper, the sophisticated falsifica-
tionist. The real Popper developed from dogmatic to a naive version of
methodological falsificationism in the twenties; he arrived at the ‘acceptance
rules’ of sophisticated falsificationism in the fifties. The transition was marked
by his adding to the original requirement of testability the ‘second’ re-
quirement of ‘independent testability’,? and then the ‘third’ requirement
that some of these independent tests should result in corroborations.* But
the real Popper never abandoned his earlier (naive) falsification rules. He
has demanded, until this day, that ‘criteria of refutation have to be laid
down beforehand: it must be agreed, which observable situations, if
actually observed, mean that the theory is refuted’.5 He still construes
‘falsification’ as the result of a duel between theory and observation, with-
out another, better theory necessarily being involved. The real Popper has
never explained in detail the appeal procedure by which some ‘accepted
basic statements’ may be eliminated. Thus the real Popper consists of
Popper, together with some elements of Poppers.

The idea of a demarcation between progressive and degenerating
problemshifts, as discussed in this paper, is based on Popper’s work:

1 Cf. my [19685].

2 Ayer seems to have been the first to attribute dogmatic falsificationism to Popper.
(Ayer also invented the myth that according to Popper ‘definite confutability’ was a criterion
not only of the empirical but also of the meaningful character of a proposition: cf. his
[1936], chapter 1, p. 38 of the second edition.) Even today, many philosophers (cf. Juhos
[1966] or Nagel [1967]) criticize the strawman Poppers. Medawar, in his [1967], called
dogmatic falsificationism ‘one of the strongest ideas’ in Popper’s methodology. Nagel,
reviewing Medawar’s book, criticized Medawar for ‘endorsing’ what he too believes to be
‘Popper’s claims’ (Nagel [1967], p. 70). Nagel’s criticism convinced Medawar that ‘the
act of falsification is not immune to human error’ (Medawar [1969], p. 54). But Medawar
and Nagel misread Popper: his Logik der Forschung is the strongest ever criticism of dog-
matic falsificationism,

One may take a charitable view of Medawar’s mistake: for brilliant scientists whose
speculative talent was thwarted under the tyranny of an inductivist logic of discovery,
falsificationism, even in its dogmatic form, was bound to have a tremendous liberating
effect. (Besides Medawar, another Nobel Prize winner, Eccles, learned from Popper to
replace his original caution by bold falsifiable speculation: cf. his [1964], pp. 274~s.)

® Popper [1957].

4 Popper [1963], pp- 242 ff.

5 Popper [1963], p. 38, footnote 3.

182 IMRE LAKATOS

indeed this demarcation is almost identical with his celebrated demarca~
tion criterion between science and metaphysics.!

Popper originally had only the theoretical aspect of problemshifts in
mind, which is hinted at in section 20 of his [1934] and developed in his
[1957].2 He added a discussion of the empirical aspect of problemshifts
only later, in his [1963].? However, Popper’s ban on ‘conventionalist
stratagems’ is in some respects too strong, in others too weak. It is too
strong, for, according to Popper, a new version of a progressive programme
never adopts a content-decreasing stratagem to absorb an anomaly, it
never says things like ‘all bodies are Newtonian except for seventeen
anomalous ones’. But since unexplained anomalies always abound, I allow
such formulations; an explanation is a step forward (that is, ‘scientific’) if it
explains at least some previous anomalies which were not explained ‘scien-
tifically’ by its predecessor. As long as anomalies are regarded as genuine
(though not necessarily urgent) problems, it does not matter much whether
we dramatize them as ‘refutations’ or de-dramatize them as ‘exceptions’:
the difference then is only a linguistic one. (This degree of tolerance of
ad hoc stratagems allows us to progress even on inconsistent foundations.
Problemshifts may then be progressive in spite of inconsistencies.*) How-
ever, Popper’s ban on content- decreasing stratagems is also too weak: it
cannot deal, for instance, with the ‘tacking paradox’,5 and does not ban
ad hoc, stratagems.* These can be eliminated only by the requirement that
the auxiliary hypotheses should be formed in accordance with the positive
heuristic of a genuine research programme. This new requirement brings us
to the problem of continuity in science.

1 If the reader is in doubt about the authenticity of my reformulation of Popper’sdemarca-
tion criterion, fe should re-read the relevant parts of Popper [1934] with Musgrave [1968]
as a guide. Musgrave wrote his [1968] against Bartley who, in his [1968], mistakenly
attributed to Popper the demarcation criterion of naive falsificationism, as formulated
above, p. 109.

2 In his [1934], Popper was primarily concerned with a ban on surreptitious ad hoc adjust-
ments. Popper (Popper,) demands that the design of a potentially negative crucial experi-
ment must be presented together with the theory, and then the verdict of the experimental
jury humbly accepted. It follows that conventionalist stratagems, which after the verdict
give a retrospective twist to the original theory in order to escape the verdict, are eo ipse
ruled out. But if we admit the refutation and then reformulate the theory with the help of
an ad hoc stratagem, we may admit it as a ‘new’ theory; and if it is testable, then Popper,
accepts it for new criticism: ‘Whenever we find that a system has been rescued by a con-
ventionalist stratagem, we shall test it afresh, and reject it, as circumstances may require’
(Popper [1934], section 20).

3 For details, cf. my [1968a], especially pp. 388-90.

“Cf, above, pp. 142 ff. This tolerance is rarely, if ever, found in textbooks of scientifiic
method.

5 Cf. above, p. 131.

8 Cf. above, p. 175, footnote 3.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 183

The problem of continuity in science was raised by Popper and his
followers long ago. When I proposed my theory of growth based on the
idea of competing research programmes, I again followed, and tried to
improve, Popperian tradition. Popper himself, in his [1934], had already
stressed the heuristic importance of ‘influential metaphysics’! and was
regarded by some members of the Vienna Circle as a champion of dan-
gerous metaphysics.? When his interest in the role of metaphysics revived
in the 1950s, he wrote a most interesting ‘Metaphysical Epilogue’ about
‘metaphysical research programmes’ to his Postscript: After Twenty Years
—in galleys since 1957.3 But Popper associated tenacity not with method-
ological irrefutability but rather with syntactical irrefutability. By ‘meta-
physics’ he meant syntactically specifiable statements like ‘all-some’ state-
ments and purely existential statements. No basic statements could conflict
with them because of their logical form. For instance, ‘for all metals there
is a solvent’ would, in this sense, be ‘metaphysical’, while Newton’s theory
of gravitation, taken in isolation, would not be.* Popper, in the 1950s, also
raised the problem of how to criticize metaphysical theories and suggested

1 Cf, e.g. his [1934], end of section 4; also cf. his [1968¢], p. 93. One should remember
that such importance was denied to metaphysics by Comte and Duhem. The people who
did most to reverse the anti-metaphysical tide in the philosophy and the historiography of
science were Burtt, Popper and Koyré.

2 Carnap and Hempel were trying, in their reviews of the book, to defend Popper against
this charge (cf. Carnap [1935] and Hempel [1937]). Hempel wrote: ‘[Popper] stresses
strongly certain features of his approach which are common with the approach of some-
what metaphysically oriented thinkers. It is to be hoped that this valuable work will not be
misinterpreted as if it meant to allow for a new, perhaps even logically defensible, meta-
physics.’

3 A passage of this Postscript is here worth quoting: ‘Atomism is an . . . excellent example
of a non-testable metaphysical theory whose influence upon science exceeded that of many
testable theories . . . The latest and greatest so far was the programme of Fgraday, Maxwell,
Einstein, de Broglie, and Schrédinger, of conceiving the world . . , in terms of continuous
fields . .. Each of these metaphysical theories functioned, long before it became testable,
as a programme for science. It indicated the direction in which satisfactory explanatory
theories of science may be found, and it made possible something like an appraisal of the
depth of a theory. In biology, the theory of evolution, the theory of the cell, and the theory of
bacterial infection, have all played similar parts, at least for a time.In psychology, sensualism,
atomism (that is, the theory that all experiences are composed of last elements, such as,
for example, sense data) and psycho-analysis should be mentioned as metaphysical research
programmes... Even purely existential assertions have sometimes proved suggestive and
even fruitful in the history of science even if they never became part of it. Indeed, few
metaphysical theories exerted a greater influence upon the development of science than
the purely metaphysical one: “There exists a substance which can turn base metals into
gold (that is, a philosopher’s stone)”, although it is non-falsifiable, was never verified, and
is now believed by nobody.’

4 Cf. especially Popper [1934], section 66. In the 1959 edition he added a clarifying
footnote (footnote *2) in order to stress that in metaphysical “all-some’ statements the
existential quantifier must be interpreted as ‘unbounded’; but, of course, he had made this
absolutely clear already in section 15 of the original text.

184 IMRE LAKATOS

solutions. Agassi and Watkins published several interesting papers on the
role of this sort of ‘metaphysics’ in science, which all connected ‘meta-
physics’ with the continuity of scientific progress. My treatment differs
from theirs first because I go much further than they in blurring the de-
marcation between [Popper’s] ‘science’ and [Popper’s] ‘metaphysics’: I do
not even use the term ‘metaphysical’ any more. I only talk about scientific
research programmes whose hard core is irrefutable, not because of syn-
tactical but because of methodological reasons which have nothing to do
with logical form. Secondly, separating sharply the descriptive problem of
the psychologico-historical role of metaphysics from the normative problem
of how to distinguish progressive from degenerating research programmes,
I elaborate the latter problem further than they had done.

Finally, I should like to discuss the ‘Duhem-Quine thesis’, and its relation
to falsificationism.®

According to the ‘Duhem-Quine thesis’, given sufficient imagination,
any theory (whether consisting of one proposition or,of a finite conjunc-
tion of many) can be permanently saved from ‘refutation’ by some suitable
adjustment in the background knowledge in which it is embedded. As
Quine put it: ‘Any statement can be held true come what may, if we make
drastic enough adjustments elsewhere in the system ... Conversely, by
the same token, no statement is immune to revision.” Moreover, the
‘system’ is nothing less than ‘the whole of science’. ‘A recalcitrant ex-
perience can be accommodated by any of various alternative reévaluations
in various alternative quarters of the total system [including the possibility
of reévaluating the recalcitrant experience itself].’

This thesis has two very different interpretations. In its weak interpre-
tation it only asserts the impossibility of a direct experimental hit on a
narrowly specified theoretical target and the logical possibility of shaping
science in indefinitely many different ways. The weak interpretation hits
only dogmatic, not methodological, falsificationism: it only denies the
possibility of a disproof of any separate component of a theoretical system.

In its strong interpretation the Duhem-—Quine thesis excludes any
rational selection rule among the alternatives; this version is inconsistent
with all forms of methodological falsificationism. The two interpretations
have not been clearly separated, although the difference is methodologi-
cally vital. Duhem seems to have held only the weak interpretation: for

2 Cf especially his [1963], pp. 198-9 (first published in 1958).

2 Cf. Watkins [1957] and [1958] and Agassi [1962] and [1964].

3 This concluding part of the Appendix was added in print.

* Quine [1953], chapter ii. 5 Ibid, The clause in the square brackets is mine.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 185

him the selection is a matter of ‘sagacity’: we must always make the right
choices in order to get nearer to ‘natural classification’.1 On the other hand,
Quine, in the tradition of the American pragmatism of James and Lewis,
seems to hold a position very near to the strong interpretation.”

Let us now have a closer look at the weak Duhem—Quine thesis. Let us
take a ‘recalcitrant experience’ expressed in an ‘observation statement’ O’
which is inconsistent with a conjunction of theoretical (and ‘observational’)
statements fy, hg...hn, Ij, I,...In, where h; are theories and J, the
corresponding initial conditions. In the ‘deductive model’, h,... hn;
I, ..-In logically imply O; but O’ is observed which implies not-O. Let
us also assume that the premisses are independent and are all necessary for
deducing O.

In this case we may restore consistency by altering any of the sentences
in our deductive model. For instance, let 4, be: ‘whenever a thread is loaded
with a weight exceeding that which characterizes the tensile strength of the
thread, then it will break’; let 4, be: ‘the weight characteristic for this
thread is 1 Jb.’; let hg be: ‘the weight put on this thread was 2 dbs’. Let,
finally, h, be: ‘an iron weight of 2 lbs was put on the thread located in the
space-time position P and it did not break’. One may solve the problem
in many ways. To give a few examples: (1) We reject 4,; we replace the
expression ‘is loaded with a weight’ by ‘is pulled by a force’; we introduce
a new initial condition: there was a hidden magnet (or hitherto unknown
force) located in the laboratory ceiling. (2) We reject h,; we propose that
the tensile strength does depend on how moist threads are; the tensile
strength of the actual thread, since it got moist, was 2 dbs. (3) We reject
hg; the weight was only 1 1b; the scales went wrong. (4) We reject hy; the
thread did not break; it was only observed to break, but the professor who
proposed h, & h, & h, was a well-known bourgeois liberal and his revolu-
tionary laboratory assistants consistently saw his hypotheses refuted when
in fact they were confirmed. (5) We reject 4,; the thread was not a ‘thread’,
but a ‘superthread’, and ‘superthreads’ never break. We could go on

1 An experiment, for Duhem, can never alone condemn an isolated theory (such as the
hard core of a research programme): for such ‘condemnation’ we also need ‘common sense’,
‘sagacity’, and, indeed, good metaphysical instinct which leads us towards (or fo) ‘a certain
supremely eminent order’. (See the end of the Appendix of the second edition of his [1906].)

2 Quine speaks of statements having ‘varying distances from a sensory periphery’,
and thus more or less exposed to change. But both the sensory periphery and the metric
are hard to define. According to Quine ‘the considerations which guide [man] in warping his
scientific heritage to fit his continuing sensory peripheries are, where rational, pragmatic’
(Quine [1953]). But ‘pragmatism’ for Quine, as for James or LeRoy, is only psychological
comfort; and I find it irrational to call this ‘rational’.

’ For such ‘concept-narrowing defences’ and ‘concept-stretching refutations’, cf.

my [1963-64].
7

186 IMRE LAKATOS

indefinitely. Indeed, there are infinitely many possibilities of how to
replace—given sufficient imagination—any of the premisses (im the de-
ductive model) by invoking a change in some distant part of our total know-
ledge (outside the deductive model) and thereby restore consistency.

Can we formulate this trivial observation by saying that ‘each test is a
challenge to the whole of our knowledge’? I do not see any reason why not.
The resistance of some falsificationists to this ‘holistic dogma of the
“global” character of all tests’! is due only to a semantic conflation of two
different notions of ‘test’ (or ‘challenge’) which a recalcitrant experimental
result presents to our knowledge.

The Popperian interpretation of a ‘test’ (or ‘challenge’) is that the result
(O) contradicts (‘challenges’) a finite, well-specified conjunction of prem-
isses (J): O & T cannot be true. But no protagonist of the Duhem—Quine
argument would deny this point.

The Quinean interpretation of ‘test’ (or ‘challenge’) is that the replacement
of O & T may invoke some change also outside O and 7. The successor
to O & T may be inconsistent with some H in some distant part of know-
ledge. But no Popperian would deny this point.

The conflation of the two notions of testing led to some misunderstand-
ings and logical blunders. Some people felt intuitively that the modus
tollens from refutation may ‘hit’ very distant premisses in our total know-
ledge and therefore were trapped in the idea that the ‘ceteris paribus clause’
is a premiss which is joined conjunctively with the obvious premisses. But
this ‘hit’ is achieved not by modus tollens but as a result of our subsequent
replacement of our original deductive model.”

Thus ‘Quine’s weak thesis’ trivially holds. But ‘Quine’s strong thesis’
will be strenuously opposed, both by the naive and the sophisticated
falsificationist.

The naive falsificationist insists that if we have an inconsistent set of
scientific statements, we first must select from among them (1) a theory
under test (to serve as a mut); then we must select (2) an accepted basic
statement (to serve as a hammer) and the rest will be uncontested back-
ground knowledge (to provide an anvil). And in order to put teeth into
this position, we must offer a method of ‘hardening’ the ‘hammer’ and the
‘anvil’ in order to enable us to crack the ‘nut’, and thus perform a ‘negative

1 Popper [1963], chapter 10, section xvi.

2 The locus classicus of this confusion is Canfield’s and Lehrer’s wrongheaded criticism
of Popper in their [1961]; Stegmiiller followed them into the logical morass ([1966], p. 7).
Coffa contributed to the clarification of the issue ([1968]).

Unfortunately, my own phraseology in this paper in places suggests that the ‘ceteris
paribus clause’ is an independent premiss in the theory under test. My attention was drawn
to this easily repairable defect by Colin Howson.

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 187

crucial experiment’. But naive ‘guessing’ of this division is too arbitrary,
it does not give us any serious hardening. (Griinbaum, on the other hand,
swallowing his falsificationist pride, stoops down to accept help from the
inductivist Salmon. He now applies Salmon’s Reichenbachian theory of
probability of hypotheses in order to show that, at least in some sense, the
‘hammer’ and the ‘anvil’ have high posterior probabilities and therefore are
‘hard’ enough for being used as a nutcracker.)

The sophisticated falsificationist allows any part of the body of science to
be replaced but only on the condition that it is replaced in a ‘progressive’
way, so that the replacement successfully anticipates novel facts. In his
rational reconstruction of falsification ‘negative crucial experiments’ play
no role. He sees nothing wrong with a group of brilliant scientists con-
spiring to pack everything they can into their favourite research programme
(‘conceptual framework’, if you wish) with a sacred hard core. As long as.
their genius—and luck—enables them to expand their programme ‘pro-
gressively’, while sticking to its hard core, they are allowed to do it. And if a
genius comes determined to replace (‘progressively’) a most uncontested
and corroborated theory which he happens to dislike on philosophical,
aesthetic or personal grounds, good luck to him. If two teams, pursuing
rival research programmes, compete, the one with more creative talent is
likely to succeed—unless God punishes them with an extreme lack of
empirical success. The direction of science is determined primarily by
human creative imagination and not by the universe of facts which sur-
rounds us. Creative imagination is likely to find corroborating novel evi-
dence even for the most ‘absurd’ programme, if the search has sufficient
drive.2 This look-out for new confirming evidence is perfectly permissible.
Scientists dream up phantasies and then pursue a highly selective hunt for
new facts which fit these phantasies. This process may be described as

1 Griinbaum [1969]. He previously took a position which was one of radical dogmatic
falsificationism and claimed that we can ascertain the falsity of scientific hypotheses
(e.g. Griinbaum [1959] and [1960]). His concrete case studies were thought-provoking
for the philosopher and challenging for the physicist. But after criticisms from Feyerabend
(cf. his [1959]), Laudan (cf. his [1965]), and others, he had to modify his position: such
falsification cannot always be ‘ascertained irrevocably’: ‘At least in some cases, we can
ascertain the falsity of a component hypothesis to all scientific intents and purposes,
although we cannot falsify it beyond any and all possibility of subsequent rehabilitation.’

2 A typical such example is Newton’s principle of gravitational attraction according
to which bodies attract each other instantly from immense distances. Huyghens described
this idea as ‘absurd’, Leibnitz as ‘occult’, and the best scientists of the age ‘wondered how
[Newton] could have given himself all the trouble of making such a number of investiga-
tions and difficult calculations that had no other foundation than this very principle’
(cf. Koyré [1965], pp. 117-18). I had argued earlier that it is not so that theoretical progress
is the merit of the theoretician but empirical] success is merely a matter of luck. If the theore-
tician is more imaginative, it is likelier that his theoretical programme will achieve at least
some empirical success. Cf. my [1968a], pp. 387-90.

188 IMRE LAKATOS

‘science creating its own universe’ (as long as one remembers that ‘creating’
here is used in a provocative-idiosyncratic sense). A brilliant school of
scholars (backed by a rich society to finance a few well-planned tests) might
succeed in pushing any fantastic programme ahead, or, alternatively, if so
inclined, in overthrowing any arbitrarily chosen pillar of ‘established
knowledge’.

The dogmatic falsificationist will throw up his hands in horror at this
approach. He will see the spectre of Bellarmino’s instrumentalism arising
from the rubble under which Newtonian success of ‘proven science’ had
buried it. He will accuse the sophisticated falsificationist of building arbi-
trary Procrustean pigeon hole systems and forcing the facts into them. He
may even brand it as a revival of the unholy irrationalist alliance of James’s
crude pragmatism and of Bergson’s voluntarism, triumphantly vanquished
by Russell and Stebbing.! But our sophisticated falsificationism combines
‘instrumentalism’ (or ‘conventionalism’) with a strong empiricist require-
ment, which neither medieval ‘saviours of phenomena’ like Bellarmino, nor
pragmatists like Quine and Bergsonians like Le Roy, had appreciated: the
Leibnitz-Whewell-Popper requirement that the—well planned—building
of pigeon holes must proceed much faster than the recording of facts which are
to be housed in them. As long as this requirement is met, it does not matter
whether we stress the ‘instrumental’ aspect of imaginative research pro-
grammes for finding novel facts and for making trustworthy predictions,
or whether we stress the putative growing Popperian ‘verisimilitude’ (that
is, the estimated difference between the truth-content and falsity-content)
of their successive versions,? Sophisticated falsificationism thus combines
the best elements of voluntarism, pragmatism and of the realist theories of
empirical growth.

The sophisticated falsificationist sides neither with Galileo nor with
Cardinal Bellarmino. He does not side with Galileo, for he claims that our
basic theories may all be equally absurd and unverisimilar for the divine
mind: and he does not side with Bellarmino, unless the Cardinal were to
agree that scientific theories may yet lead, in the long run, to ever more true
and ever fewer false consequences and, in this strictly technical sense, may
have increasing ‘verisimilitude’.®

1Cf. Russell [1914], Russell [1946] and Stebbing [1914]. Russell, a justificationist,
despised conventionalism: ‘As will has gone up in the scale, knowledge has gone down.
This is the most notable change that has come over the temper of philosophy in our age.
It was prepared by Rousseau and Kant...’ ([1946], p. 787). Popper, of course, got some
of his inspiration from Kant and Bergson. (Cf. his [1934], sections 2 and 4.)

2 Cf. Popper [1963], chapter 10.

8Verisimilitude’ has two distinct meanings which must not be conflated. First, it may be
used to mean intuitive truthlikeness of the theory; in this sense, in my view, all scientific
theories created by the human mind are equally unverisimilar and ‘occult’. Secondly, it

METHODOLOGY OF SCIENTIFIC RESEARCH PROGRAMMES 189

may be used to mean the set-theoretical difference between the true and false consequences
of a theory which we can never know but certainly may guess. It was Popper who used
‘verisimilitude’ as a precise technical term to denote this difference ([1963], chapter 10),
But his claim that this explication corresponds closely to the original meaning is mistaken
and misleading. In the original prepopperian usage ‘verisimilitude’ could mean either
intuitive truthlikeness or a naive proto-version of Popper’s empirical truthlikeness. Popper
gives interesting quotations for the latter ([1963], pp. 399 ff.) but none for the former,
But Bellarmino might have agreed that Copernican theory had high ‘verisimilitude’ in
Popper’s technical sense but not that it had verisimilitude in the first, intuitive sense.
Most ‘instrumentalists’ are ‘realists’ in the sense that they agree that the [Popperian]
‘verisimilitude’ of scientific theories is likely to be growing; but they are not ‘realists’ in the
sense that they would agree that, for instance, the Einsteinian field approach is intuitively
closer to the Blueprint of the Universe than the Newtonian action at a distance. The ‘aim
of science’ may then be increasing Popperian ‘verisimilitude’, but does not have to be also in-
creasing classical verisimilitude. The latter, as Popper himself said, is, unlike the former,
a ‘dangerously vague and metaphysical’ idea ([1963], p. 231).

Popper’s ‘empirical verisimilitude’ in a sense rehabilitates the idea of cumulative growth
in science. But the driving force of cumulative growth in ‘empirical verisimilitude’ is revo-
lutionary conflict in ‘intuitive verisimilitude’,

When Popper was writing his ‘Truth, rationality and the growth of knowledge’, I had
an uneasy feeling about his identification of the two concepts of verisimilitude. Indeed, it
was I who asked him: ‘Can we really speak about better correspondence? Are there such
things as degrees of truth? Is it not dangerously misleading to talk as if Tarskian truth were
located somewhere in a kind of metrical or at least topological space so that we can sensibly
say of two theories—say an earlier theory f, and a later theory ¢,, that t, has superseded
t,, or progressed beyond #,, by approaching more closely to the truth than #,?’ (Popper
[1963], p. 232). Popper rejected my vague misgivings. He felt—rightly—that he was
proposing a very important new idea. But he was mistaken in believing that his new,
technical conception of ‘verisimilitude’ completely absorbed the problems centred on the
old intuitive ‘verisimilitude’. Kuhn says: “To say, for example, of a field theory that it
“approaches more closely to the truth” than an older matter-and-force theory should
mean, unless words are being oddly used, that the ultimate constituents of nature are more like
fields than like matter and force’ (this volume, below, p. 265; my italics). Indeed, Kuhn
is right, except that words are normally ‘oddly used’. I hope that this note may contribute
to the clarification of the problem involved.

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Consolations for the Specialist’

PAUL FEYERABEND
University of California, Berkeley

‘I have been hanging people for years, but I have never had all this fuss before.’
(Remark made by Edward ‘Lofty’ Milton, Rhodesia’s part time executioner on the
occasion of demonstrations against the death penalty.) ‘He was’—says Time Maga-
zine (15 March 1968)—‘professionally incapable of understanding the commotion.’

Introduction.

Ambiguity of presentation.

Puzzle solving as a criterion of science.

Function of normal science.

Three difficulties of functional argument.

Does normal science exist?

A plea for hedonism.

An alternative: the Lakatos model of scientific change.
The role of reason in science.

ND: OO ese ON ot

I INTRODUCTION

In the years 1960 and 1961 when Kuhn was a member of the philosophy
department at the University of California in Berkeley I had the good
fortune of being able to discuss with him various aspects of science. I have
profited enormously from these discussions and I have looked at science in
a new way ever since.” Yet while I thought I recognized Kuhn’s problems;
and while I tried to account for certain aspects of science to which he had
drawn attention (the omnipresence of anomalies is one example); I was
quite unable to agree with the theory of science which he himself proposed ;
and I was even less prepared to accept the general ideology which I thought
formed the background of his thinking. This ideology, so it seemed to me,
could only give comfort to the most narrowminded and the most con-
ceited kind of specialism. It would tend to inhibit the advancement of
knowledge. And it is bound to increase the anti-humanitarian tendencies

1 An earlier version of this paper was read in Professor Popper’s seminar at the London
School of Economics (March 1967). I would like to thank Professor Popper for this oppor-
tunity as well as for his own detailed criticism. I am also grateful to Messrs Howson and
Worrall for their valuable editorial and stylistic help.

2 The criticism of some features of contemporary methodology which appears in my
[1969] and [1970] is but one belated after-effect.

197

198 PAUL FEYERABEND

which are such a disquieting feature of much of post-Newtonian science.!
On all these points my discussions with Kuhn remained inconclusive.
More than once he interrupted a lengthy sermon of mine, pointing out
that I had misunderstood him, or that our views are closer than I had made
them appear. Now, looking back at our debates? as well as at the papers
which Kuhn has published since his departure from Berkeley, I am not so
sure that this was the case. And I am fortified in my behalf by the fact that
almost every reader of Kuhn’s Structure of Scientific Revolutions interprets
him as I do, and that certain tendencies in modern sociology and modern
psychology are the result of exactly this kind of interpretation. I hope that
Kuhn will forgive me when therefore I once more raise the old issues and
that he will not take it amiss when in my effort to be brief I do this in a
somewhat blunt fashion.

2. AMBIGUITY OF PRESENTATION

Whenever I read Kuhn, I am troubled by the following question: are we
here presented with methodological prescriptions which tell the scientist
how to proceed; or are we given a description, void of any evaluative
element, of those activities which are generally called ‘scientific’? Kuhn’s
writings, it seems to me, do not lead to a straightforward answer. They are
ambiguous in the sense that they are compatible with, and lend support to,
both interpretations. Now this ambiguity (whose stylistic expression and
mental impact has much in common with similar ambiguities in Hegel
and in Wittgenstein) is not at all a side issue. It has had quite a definite
effect on Kuhn's readers and has made them look at, and deal with their
subject in a manner not altogether advantageous. More than one social
scientist has pointed out to me that now at last he had learned how to turn
his field into a ‘science’-—by which of course he meant that he had learned
how to improve it. The recipe, according to these people, is to restrict
criticism, to reduce the number of comprehensive theories to one, and to
create a normal science that has this one theory as its paradigm.*® Students
must be prevented from speculating along different lines and the more
restless colleagues must be made to conform and ‘to do serious work’. Is this
what Kuhn wants to achieve? Is it his intention to provide a historico-

1 Cf. my [1970].

® Some of which were carried out in the now defunct Café Old Europe on Telegraph
Avenue and greatly amused the other customers by their friendly vehemence.

3 See, e.g. Reagan [1967] p. 1385: He states: ‘We [that is, we social scientists] are in
what Kuhn might call a “pre-paradigm”’ stage of development in which consensus has yet
to emerge on basic concepts and theoretical assumptions.’

4 Neurophysiology, physiology, and certain parts of psychology are far ahead of con-
temporary physics in that they manage to make the discussion of fundamentals an essential
part of even the most specific piece of research. Concepts are never completely stabilized

CONSOLATIONS FOR THE SPECIALIST 199

scientific justification for the ever growing need to identify with some
group? Does he want every subject to imitate the monolithic character of,
say, the quantum theory of 1930? Does he think that a discipline that has
been constructed in this manner is in some ways better off? That it will
lead to better, to more numerous, to more interesting results? Or is his
following among sociologists an unintended side-effect of a work whose
sole purpose is to report ‘wie es wirklich gewesen’ without implying that the
reported features are worthy of imitation? And if this is the sole purpose of
the work, then why the constant misunderstanding, and why the ambiguous
and occasionally highly moralizing style?

I venture to guess that the ambiguity is intended and that Kuhn wants to
fully exploit its propagandistic potentialities. He wants on the one side to
give solid, objective, historical support to value judgements which he just
as many other people seem to regard as arbitrary and subjective. On the
other side he wants to leave himself a safe second line of retreat: those who
dislike the implied derivation of values from facts can always be told that
no such derivation is made and that the presentation is purely descriptive.
My first set of questions, therefore, is: why the ambiguity? How is it to be
interpreted? What is Kuhn’s attitude towards the kind of following I have
described? Have they misread him? Or are they legitimate followers of a
new vision of science?

3. PUZZLE SOLVING AS A CRITERION OF SCIENCE

Let us now disregard the problem of presentation and let us assume that
Kuhn’s aim is indeed to give but a description of certain influential his-
torical events and institutions.

According to this interpretation it is the existence of a puzzle-solving
tradition that de facto sets the sciences apart from other activities. It sets
them apart in a ‘far surer and more direct’ way, in a manner that 1s ‘at
once... less equivocal and...more fundamental’,! than do other and
more recondite properties which they may also possess. But if the existence

but are left open and are elucidated now by the one, now by the other theory. There is no
indication that progress is hampered by the more ‘philosophical’ attitude which, according
to Kuhn, underlies such a procedure (cf. this volume, p. 6). (Thus the lack of clarity about
the idea of perception has led to many interesting empirical investigations, some of them
yielding quite unexpected and highly important results. Cf. Epstein [1967], especially
pp. 6-18.) Quite the contrary, we find a greater awareness of the limits of our knowledge,
of its connection with human nature, we find also a greater familiarity with the history of
the subject and the ability not only to record, but to actively use past ideas for the advance-
ment of contemporary problems. Must we not admit that all this contrasts most favourably
with the humourless dedication and the constipated style of a ‘normal’ science?
1 Cf. this volume, p. 7.

200 PAUL FEYERABEND

of a puzzle-solving tradition is so essential, if it is the occurrence of this
property that unifies and characterizes a specific and well recognizable
discipline; then I do not see how we shall be able to exclude say, Oxford
philosophy, or, to take an even more extreme example, organized crime
from our considerations.

For organized crime, so it would seem, is certainly puzzle-solving par
excellence, Every statement which Kuhn makes about normal science re-
mains true when we replace ‘normal science’ by ‘organized crime’; and
every statement he has written about the ‘individual scientist’ applies with
equal force to, say, the individual safebreaker.

Organized crime certainly keeps foundational research to a minimum?
although there are outstanding individuals, suchas Dillinger, who introduce
new and revolutionary ideas.2 Knowing the rough outlines of the pheno-
mena to be expected the professional safebreaker ‘largely ceases to be an
explorer . . . or at least an explorer of the unknown [after all, he is supposed
to know all the existing types of safe]. Instead, he struggles to... con-
cretize the known fi.e. to discover the idiosyncracies of the particular safe
he is dealing with], designing much special-purpose apparatus and many
special-purpose adaptations of theory for that task’.? According to Kuhn
failure of achievement most certainly reflects ‘on the competence of the
(safebreaker] in the eyes of his professional compeers” so that ‘it is the
individual [safebreaker] rather than current theory [of electromagnetism,
for example] which is tested’*: ‘only the practitioner is blamed, not his
tools’’—and so we can continue step for step, down to the very last item
on Kuhn’s list. The situation is not improved by pointing to the existence
of revolutions. First of all, because we are dealing with the thesis that it is
normal science which is characterized by the activity of puzzle-solving.
And secondly because there is no reason to believe that organized crime
will fall behind in the mastery of major difficulties. Besides, if it is the
pressure derived from the ever increasing number of anomalies that leads,
first to a crisis, and then to a revolution, then the greater the pressure, the
sooner the crisis must occur. Now the pressure exerted upon the members
of a gang and their ‘professional compeers’ certainly can be expected to
exceed the pressures upon a scientist—the latter hardly ever has to deal
with the police. Wherever we look—the distinction we want to draw does
not exist.

3 Cf. Kuhn [19614], p. 357.

® Dillinger considerably advanced the technique of the bank-holdup by staging dress
rehearsals in life size models of the target-banks which he built at his farm. He thereby
refuted Andrew Carnegie’s ‘Pioneering don’t pay’.

* Kuhn [19614], p. 363. 4 This volume, p. 9; also cf. p. 7 and footnote 1 on p. 5.
& This volume, p. 5. ® This volume, p. '7; also cf. Kuhn [1962], p. 79.

CONSOLATIONS FOR THE SPECIALIST 201

This of course is no surprise. For Kuhn, as we interpret him now and as
he himself very often wants to be interpreted, has failed to do one impor-
tant thing. He has failed to discuss the aim of science. Every crook knows
that apart from succeeding at his trade and being popular with his fellow
crooks he wants one thing: money. He also knows that his normal criminal
activity is going to give him just this. He knows that he will receive the
more money and rise the faster on the professional ladder the better he is as
a puzzle-solver and the better he fits into the criminal community. Money
is his aim. What is the aim of the scientist? And, considering this aim, is
normal science going to lead up to it? Or are perhaps scientists (and Oxford
philosophers) less rational than crooks in that they ‘are doing what they
are doing’ without regard to an aim?! These are the questions which arise
if one wants to restrict oneself to the purely descriptive aspect of Kuhn’s
account.

4. FUNCTION OF NORMAL SCIENCE

In order to answer these questions we must now consider not only the
actual structure of Kuhnian normal science, but also its function. Normal
science, he says, is a necessary presupposition of revolutions.

According to this part of the argument the pedestrian activity associated
with ‘mature’ science has far reaching effects both upon the content of our
ideas, and upon their substantiality. This activity, this concern with ‘tiny
puzzles’ leads to a close fit between theory and reality, and it also precipi-
tates progress. It does so for various reasons. First of all the accepted
paradigm gives the scientist a guide: ‘As a glance at any Baconian natural
history or a survey of the pre-paradigm development of any science will
show, nature is vastly too complex to be explored even approximately at
random’.? This point is not new. The attempt to create knowledge needs
guidance, it cannot start from nothing. More specifically, it needs a theory,
a point of view that allows the researcher to separate the relevant from the
irrelevant, and that tells him in what areas research will be most profitable.

To this common idea Kuhn adds a specific twist of his own. He defends
not only the use of theoretical assumptions, but the exclusive choice of one
particular set of ideas, the monomaniac concern with only one single point
of view. He defends such a procedure first, because it plays a role in actual
science as he sees it. This is the description-recommendation ambiguity
already dealt with. But he defends it also for a second reason that is some-
what more recondite as the preferences behind it are not made explicit.
He defends it because he believes that its adoption will in the end lead to the

1*T am doing what I am doing’ was a favourite remark of Austin’s.
2 Kuhn [1961a], p. 363.

202 PAUL FEYERABEND

overthrow of the very same paradigm to which the scientists have restricted
themselves in the first place. If even the most concerted effort to fit nature
into its categories fails; if the very definite expectations created by these
categories are disappointed again and again; then we are forced to look for
something new. And we are forced to do this not just by an abstract dis-
cussion of possibilities which does not touch reality, but is rather guided
by our own likes and dislikes’; we are forced to do it by procedures which
have established a close contact with nature, and therefore, in the last
resort, by nature itself. The debates of pre-science with their universal
criticism and their uninhibited proliferation of ideas are ‘often directed as
much to the members of other schools as... to nature’.? Mature science,
especially in the quiet periods immediately before the storm, seems to
address nature itself only and may therefore expect a definite and objective
answer. In order to get such an answer we need more than a collection of
facts assembled at random, But we need also more than an everlasting
discussion of different ideologies. What is needed is the acceptance of one
theory and the relentless attempt to fit nature into its pattern. This, I
think, is the main reason why the rejection, by a mature science, of the
uninhibited battle between alternatives would be defended by Kuhn not
only as a historical fact, but also as a reasonable move. Is this defence
acceptable?

5. THREE DIFFICULTIES OF FUNCTIONAL ARGUMENT

Kuhn’s defence is acceptable provided revolutions are desirable and pro-
vided the particular way in which normal science leads to revolutions is
desirable also.

Now I do not see how the desirability of revolutions can be established
by Kuhn. Revolutions bring about a change of paradigm. But following
Kuhn’s account of this change, or ‘gestalt-switch’ as he calls it, it is impos-
sible to say that they have led to something better. It is impossible to say
this because pre- and post-revolutionary paradigms are frequently incom-
mensurable.® This I would regard as the first difficulty of the functional
argument if used in connection with the remainder of Kuhn’s philosophy.

Secondly we have to examine what Lakatos has called the ‘fine-structure’
of the transition: normal science/revolution. This fine-structure may
reveal elements we do not want to condone. Such elements would force us

1‘If any one offers conjectures about the truth of things from the mere possibility of
hypothesis, then I do not see how any certainty can be determined in any science; for it is
always possible to contrive hypotheses, one after another, which are found to lead to new
difficulties’ (Newton [1672)]).

4 Kuhn [1962], p. 13.

3 Cf. below, section 9.

CONSOLATIONS FOR THE SPECIALIST 203

to consider different ways of bringing about a revolution. Thus it is quite
imaginable that scientists abandon a paradigm out of frustration and not
because they have arguments against it. (Killing the representatives of the
status quo would be another way of breaking up a paradigm.') How do
scientists actually proceed? And how would we want them to proceed? An
examination of these questions leads to a second difficulty for the functional
argument.

In order to exhibit this difficulty as clearly as possible let us first con-
sider the following methodological problems: Is it possible to give reasons for
proceeding as Kuhn says normal science proceeds, that is, for trying to
stick to a theory despite the existence of prima facie refuting evidence, of
logical, and of mathematical counter arguments? And assuming it is pos-
sible to give such reasons—is it then possible to abandon the theory with-
out violating them?

In what follows I shall call the advice to select from a number of theories
the one that promises to lead to the most fruitful results, and to stick to this
one theory even if the actual difficulties it encounters are considerable,
the principle of tenacity." The problem then is how this principle can be

1This is how religious doctrines or political doctrines were frequently replaced. The
principle remains even today, though murder is no longer the accepted method, The
reader should also consider Max Planck’s remark that old theories disappear because
their defenders die out.

* This formulation of the principle was suggested by an objection which Isaac Levi
raised against an earlier version.

The principle of tenacity as formulated in the text should not be confused with Putnam’s
rule of tenacity (Putnam [1963], p. 772). For while Putnam’s rule demands that a theory
should be retained ‘unless it becomes inconsistent with the data’ (his italics) tenacity as
understood by Kuhn and by myself demands that it should be retained even if there are
data which are inconsistent with it. This stronger version creates problems which do not
appear in Putnam’s methodology and which, I suggest, can be solved only if one is prepared
to use a multiplicity of mutually inconsistent theories at any time of the development of our
knowledge. It seems to me that neither Kuhn not Putnam is prepared to take this step.
But while Kuhn sees the need for the use of alternatives (see below) Putnam demands that
their number be always reduced either to one or to zero (ibid. pp. 770 fif.).

Lakatos differs from the account given in the text above in two respects. He distinguishes
between theories and research programmes. And he applies tenacity to research programmes
only.

Now while I admit that the distinction and the use he makes of it may increase clarity,
I am still inclined to stick to my own and much more vague term ‘theory’ (for a partial
explanation of this term, cf. my footnote 5 [1965a]) which covers both Lakatos’s ‘theories’
and ‘research programmes’, to connect it with tenacity, and to altogether eliminate the
more simple forms of refutation. One reason for this preference is given by Lakatos
himself who has shown that even simple refutations involve a plurality of theories (see
especially his paper in this volume, pp. 121 ff.). Another reason is my belief that progress can
be brought about only by the active interaction of different ‘theories’ which of course
assumes that the ‘research programme’-component comes forth not only occasionally,
but is present all the time (cf. also below, section 9).

204 PAUL FEYERABEND

defended, and how we can change our allegiance to paradigms in a manner
that is either consistent with it, or perhaps even dictated by it. Remember
that we are here dealing with a methodological problem and not with the
question of how science actually proceeds. We are dealing with it because
we hope that its discussion will sharpen our historical perception and will
lead us to interesting historical discoveries.

Now the solution of the problem is quite straightforward. The principle
of tenacity is reasonable because theories are capable of development,
because they can be improved, and because they may eventually be able to
accommodate the very same difficulties which in their original form they
were quite incapable of explaining. Besides, it is not at all prudent to put
too much trust in experimental results. Indeed, it would be a complete
surprise and even a cause for suspicion, if all the available evidence should
turn out to support a single theory, even if this theory should happen to be
true. Different experimenters are liable to commit different errors and it
usually needs considerable time before all experiments are brought to a
common denominator.! To these arguments in favour of tenacity Pro-
fessor Kuhn would add that a theory also provides criteria of excellence,
of failure, of rationality, and that one must support it as long as possible,
in order to keep the discourse rational as long as possible. The most impor-
tant point is however this: it is hardly ever the case that theories are
directly compared with ‘the facts’, or with ‘the evidence’. What counts
and what does not count as relevant evidence usually depends on the
theory as well as on other subjects which may conveniently be called
‘auxiliary sciences’ (‘touchstone theories’ is Imre Lakatos’s apt expression’).
Such auxiliary sciences may function as additional premises in the deriva-
tion of testable statements. But they may also infect the observation
language itself, providing the very concepts in terms of which experi-
mental results are expressed. Thus a test of the Copernican view involves
on the one hand assumptions concerning the terrestrial atmosphere, the
effect of motion upon the object moved (dynamics); and on the other it
also involves assumptions about the relation between sense experience
and ‘the world’ (theories of cognition, theories of telescopic vision in-
cluded).

The former assumptions function as premises while the latter determine
which impressions are veridical and thus enable us not only to evaluate,
but even to constitute our observations. Now there is no guarantee that a
fundamental change in our cosmology, such as a change from a geostatic

1 It took about twenty-five years before the disturbances of D. C. Miller’s repetition of
the Michelson—Morley experiment were accounted for in a satisfactory manner. H. A.
Lorentz had given up in despair long before that time. 2 Cf. his [1968a].

CONSOLATIONS FOR THE SPECIALIST 205

to a heliostatic point of view, will go hand in hand with an improvement of
all the relevant auxiliary subjects. Quite the contrary: such a development
is extremely unlikely. Who for example would expect the invention of
Copernicanism and of the telescope to be at once followed by the approp-
riate physiological optics? Basic theories and auxiliary subjects are often
‘out of phase’. As a result we obtain refuting instances which do not indi-
cate that a new theory is doomed to failure, but only that it does not fit in
at present with the rest of science. This being the case scientists must
develop methods which permit them to retain their theories in the face of
plain and unambiguously refuting facts, even if testable explanations for
the clash are not immediately forthcoming. The principle of tenacity
(which I call a ‘principle’ for mnemonic reasons only) is a first step in the
construction of such methods.!

Having adopted tenacity we can no longer use recalcitrant facts for
removing a theory, 7, even if the facts should happen to be as plain and
straight-forward as daylight itself. But we can use other theories, 7’, T”,
T’"’, etc. which accentuate the difficulties of J while at the same time
promising means for their solution. In this case elimination of T is urged
by the principle of tenacity itself.? Hence, if change of paradigms is our
aim, then we must be prepared to introduce and articulate alternatives to
T or, as we shall express it (again for mnemonical reasons), we must be
prepared to accept a principle of proliferation. Proceeding in accordance
with such a principle is one method of precipitating revolutions. It is a
rational method. Is it the method which science actually uses? Or do
scientists stick to their paradigms to the bitter end until disgust, frustra-
tion and boredom makes it quite impossible for them to go on? What does
happen at the end of a normal period? We see that our little methodological
fairytale makes us indeed look at history with a sharpened vision.

I am sorry to say that I am quite dissatisfied with what Kuhn has to
offer on this point. On the one side he steadfastly emphasizes the dog-
matic,® authoritarian,* and narrowminded® features of normal science, the
fact that it leads to a temporary ‘closing of the mind’,® that the scientist
participating in it ‘largely ceases to be an explorer . . . or at least an explorer
of the unknown. Instead, he struggles to articulate and concretize the

1 For details concerning the ‘phase difference’ between theories and the corresponding
auxiliary sciences, cf. my [1969]. The idea already occurs in Lakatos’s [1963-4]; it is a
commonplace for Lenin and Trotsky (cf. my [1969]).

2 This is of course not the whole story—but the present sketch suffices entirely for our
purpose. Note that Kuhn’s argument for tenacity (need for a rational background of
argument) is not violated either as the better theory will of course also provide better
standards of rationality and excellence. 3 Kuhn [r96ral], p. 349.

4 Ibid. p. 393. 5 Ibid. p. 350. 5 Ibid. p. 393.

206 PAUL FEYERABEND

known ...’! so that ‘it is [almost always] the individual scientist rather
than [the puzzle-solving tradition, or even some particular] current theory
which is tested’.2 ‘Only the practitioner is blamed, not his tools.’* He
realizes of course that a specific science such as physics may contain more
than one puzzle-solving tradition, but he emphasizes their ‘quasi-inde-
pendence’, asserting that each of them is ‘guided by its own paradigms and
pursuing its own problems’.* A single tradition therefore will be guided
by a single paradigm only. This is one side of the story.

On the other side he points out that puzzle solving is replaced by more
‘philosophical’ arguments as soon as there exists a choice ‘between com-
peting theories’.®

Now if normal science is de facto as monolithic as Kuhn makes it out to
be, then where do the competing theories come from? And if they do arise,
then why should Kuhn take them seriously and allow them to bring about
a change of the argumentative style, from ‘scientific’ (puzzle solving) to
‘philosophical’? I remember very well how Kuhn criticized Bohm for
disturbing the uniformity of the contemporary quantum theory. Bohm’s
theory is mot permitted to change the argumentative style. Einstein, whom
Kuhn mentions in the above quotation, is permitted to do so, perhaps
because his theory is now more firmly entrenched than Bohm’s. Does this
mean that proliferation is permitted as long as the competing alternatives
are firmly entrenched? But pre-science which has exactly this feature is
regarded as inferior to science. Besides, twentieth-century physics does
contain a tradition which wants to isolate the general theory of relativity
from the rest of physics, and restrict it to the very large. Why has Kuhn
not supported this tradition which is in line with his view of the ‘quasi-
independence’ of simultaneous paradigms? Conversely, if the existence
of competing theories involves a change of argumentative style, must we
not then doubt this alleged quasi-independence? I have been unable to
find a satisfactory answer to these questions in Kuhn’s writings.

Let us pursue the point a little further. Kuhn has not only admitted that
multiplicity of theories changes the style of argumentation. He has also
ascribed a definite function to such multiplicity. He has pointed out more
than once,’ in complete agreement with our brief methodological remarks,
that refutations are impossible without the help of alternatives. Moreover,

1 Kuhn [19614], p. 363.

2 This volume, p. 5.

3 This volume, p. 7; also cf. Kuhn [1962], p. 79.

“Kuhn [19614], p. 388. 5 This volume, p. 7.

4 ‘Philosophical’ in Kuhn’s (and Popper’s) sense and not in the sense of, say, contemporary
linguistic philosophy.

7 Cf. Kuhn [196108] and also my acknowledgement in my [1962], p. 32.

CONSOLATIONS FOR THE SPECIALIST 207

he has described in some detail the magnifying effect which alternatives
have upon anomalies and has explained how revolutions are brought about
by such a magnification.! He has therefore said, in effect, that scientists
create revolutions in accordance with our little methodological model and
not by relentlessly pursuing one paradigm and suddenly giving up when
the problems get too big.

All this leads now at once to difficulty number three, viz. the suspicion
that normal or ‘mature’ science, as described by Kuhn, 1s not even a his-
torical fact.

6. DOES NORMAL SCIENCE EXIST?

Let us recall what we have so far found to be asserted by Kuhn. First,
it is asserted that theories cannot be refuted except with the help of alterna-
tives. Secondly, it is asserted that proliferation also plays a Historical role
in the overthrow of paradigms. Paradigms have been overthrown because
of the way in which alternatives have enlarged existing anomalies. Finally,
Kuhn has pointed out that anomalies exist at any point of the history of a
paradigm.” The idea that theories are blameless for decades and even cen-
turies until a big refutation turns up and knocks them out—this idea, he
asserts, is nothing but a myth. Now if this is true, then why should we not
start proliferating at once and never allow a purely normal science to come
into existence? And is it too much to be hoped that scientists thought like-
wise, and that normal periods, if they ever existed, cannot have lasted very
long and cannot have extended over large fields either? A brief look at one
example, viz. the last century, shows that this seems indeed to be the
case.

In the second third of that century there existed at least three different
and mutually incompatible paradigms, They were: (1) the mechanical
point of view which found expression in astronomy, in the kinetic theory,
in the various mechanical models for electrodynamics as well as in the bio-
logical sciences, especially in medicine (here the influence of Helmholtz
was a decisive factor); (2) the point of view connected with the invention
of an independent and phenomenological theory of heat which finally
turned out to be inconsistent with mechanics; (3) the point of view implicit
in Faraday’s and Maxwell’s electrodynamics which was developed, and
freed from its mechanical concomitants, by Hertz.

1 A minor disturbance, still accessible to treatment ‘can be seen, from another viewpoint,
as a counterinstance, and thus as a source of crisis’ (Kuhn [1962], p. 79). ‘Copernicus’
astronomical proposal . . . created an increasing crisis for . . . the paradigm from which it
had sprung’ (ibid. p. 74, my italics), ‘Paradigms are not corrigible by normal science at all’
(ibid. p. 121, my italics).

2 Kuhn [1962], pp. 80 ff. and p. 145.

208 PAUL FEYERABEND

Now these different paradigms were far from being ‘quasi-independent’.
Quite the contrary, it was their active interaction which brought about the
downfall of classical physics. The troubles leading to the special theory of
relativity could not have arisen without the tension that existed between
Maxwell’s theory on the one side and Newton’s mechanics on the other
(Einstein has described the situation in beautifully simple terms in his
autobiography; Weyl has given an equally brief, though more technical
account in Raum, Zeit, Materie; Poincaré exhibits this tension already in
1899, and then again in 1904, in his St Louis lecture). Nor was it possible
to use the phenomenon of Brownian motion for a direct refutation of the
second law of the phenomenological theory. The kinetic theory had to be
introduced from the very start. Here again Einstein, following Boltzmann,
led the way. The investigations leading up to the discovery of the quantum
of action, to mention still another example, brought together such different,
incompatible, and occasionally even incommensurable disciplines as
mechanics (kinetic theory as used in Wien’s derivation of his law of radia-
tion), thermodynamics (Boltzmann’s principle of the equal distribution of
energy over all degrees of freedom) and wave optics and they would have
collapsed had the ‘quasi-independence’ of these subjects been respected by
all scientists. Of course not everyone participated in the debate and the
great majority may well have continued attending to their ‘tiny puzzles’.
However if we take seriously what Kuhn himself is teaching then it was
not this activity that brought about progress, but the activity of the pro-
liferating minority (and of those experimenters who attended to the
problems of this minority, and to their strange predictions). And we may
ask whether the majority does not continue solving the old puzzles right
through the revolutions. But if this is true then Kuhn’s account which
temporally separates periods of proliferation and periods of monism
altogether collapses.?

1 Cf. my discussion in section VI of my [19655].

2 It might be objected that the puzzle-solving activity, though not sufficient for bringing
about a revolution, is certainly necessary as it creates the material which eventually leads
to trouble: puzzle solving is responsible for some conditions on which scientific progress
depends. This objection is refuted by the Presocratics who progressed (their theories did
not just change, they were also improved) without paying the slightest attention to puzzles.
Of course, they did not produce the pattern: normal science—revolution—normal
science—revolution, etc., in which professional stupidity is periodically replaced by philo-
sophical outbursts only to return again at a ‘higher level’. However there is no doubt that
this is an advantage as it permits us to be open-minded all the time and not only in the
middle of a catastrophe. Besides—is not ‘normal science’ full of ‘facts’ and ‘puzzles’ which
belong, not to the current paradigm, but to some earlier predecessors? And is it not also the
case that anomalous facts are often infroduced by the critics of a paradigm, rather than
used by them as a starting point for criticism? And if that is true, does it not follow that it is
proliferation rather than the pattern normalcy-proliferation-normalcy that characterizes

CONSOLATIONS FOR THE SPECIALIST 209

7. A PLEA FOR HEDONISM

It seems, then, that the interplay between tenacity and proliferation
which we described in our little methodological fairytale is also an essential
feature of the actual development of science. It seems that it is not the
puzzle-solving activity that is responsible for the growth of our know-
ledge but the active interplay of various tenaciously held views. Moreover,
it is the invention of new ideas and the attempt to secure for them a worthy
place in the competition that leads to the overthrow of old and familiar
paradigms. Such inventing goes on all the time. Yet it is only during revolu-
tions that the attention turns to it. This change of attention does not reflect
any profound structural change (such as for example a transition from
puzzle solving to philosophical speculation and testing of foundations). It
is nothing but a change of interest and of publicity.

This is the picture of science that emerges from our brief analysis. Is it
an attractive picture? Does it make the pursuit of science worthwhile?
Is the presence of such a discipline, the fact that we have to live with it,
study it, understand it, beneficial to us, or is it perhaps liable to corrupt
our understanding and diminish our pleasure?

It is very difficult nowadays to approach such questions in the right
spirit. What is worthwhile and what is not are to such a large extent de-
termined by the existing institutions and forms of life that we hardly ever
arrive at a proper evaluation of these institutions themselves.! The sciences
especially are surrounded by an aura of excellence which checks any in-
quiry into their beneficial effect. Phrases such as ‘search for the truth’, or
‘highest aim of mankind’ are liberally used. Undoubtedly they ennoble
their object, but they also remove it from the domain of critical discussion
(Kuhn has gone one step further in this direction, conferring some dignity
even on the most boring and most pedestrian part of the scientific enter-
prise: normal science). Yet why should a product of human ingenuity be
allowed to put an end to the very same questions to which it owes its
existence? Why should the existence of this product prevent us from asking
the most important question of all, the question to what extent the happi-
ness of individual human beings, and to what extent their freedom, has
been increased? Progress has always been achieved by probing well-
entrenched and well-founded forms of life with unpopular and unfounded
values. This is how man gradually freed himself from fear and froin the
science? So that Kuhn’s position would be not only methodologically untenable (see the
previous section) but also historically false?

1 Modern analytic philosophers are trying to show that such evaluation is even logically

impossible, In this they are but the followers of Hegel—except that they lack his knowledge,
his comprehensiveness and his wit.

210 PAUL FEYERABEND

tyranny of unexamined systems. Our question therefore is: what values
shall we choose to probe the sciences of today?

It seems to me that the happiness and the full development of an indi-
vidual human being is now as ever the highest possible value. This value
does not exclude the values which flow from institutionalized forms of life
(truth; valour; self-negation; etc.). It rather encourages them but only to
the extent to which they can contribute to the advance of some individual.
What is excluded is the use of institutionalized values for the condemna-
tion, or perhaps even the elimination, of those who prefer to arrange their
lives in a different way. What is excluded is the attempt to ‘educate’
children in a manner that makes them lose their manifold talents so that
they become restricted to a narrow domain of thought, action, emotion.
Adopting this basic value we want a methodology and a set of institutions
which enable us to lose as little as possible of what we are capable of doing
and which force us as little as possible to deviate from our natural inclina-
tions.

Now the brief methodological fairytale which we have sketched in sec-
tion 6, says that a science that tries to develop our ideas and that uses
rational means for the elimination of even the most fundamental conjec-
tures must use a principle of tenacity together with a principle of pro-
liferation. It must be allowed to retain ideas in the face of difficulties; and
it must be allowed to introduce new ideas even if the popular views should
appear to be fully justified and without blemish. We have also found that
actual science, or at least the part of actual science that is responsible for
change and for progress, is not very different from the ideal outlined in the
fairytale. But this is a happy coincidence indeed! We are now in full agree-
ment with our wishes as expressed above! Proliferation means that there
is no need to suppress even the most outlandish product of the human
brain. Everyone may follow his inclinations and science, conceived as a
critical enterprise, will profit from such an activity. Tenacity: this means
that one is encouraged not just to follow one’s inclinations, but to develop
them further, to raise them, with the help of criticism (which involves a
comparison with the existing alternatives) to a higher level of articulation
and thereby to raise their defence to a higher level of consciousness. The inter-
play between proliferation and tenacity also amounts to the continuation,
on a new level, of the biological development of the species and it may even
increase the tendency for useful biological mutations. It may be the only
possible means of preventing our species from stagnation. This I regard as
the final and the most important argument against a ‘mature’ science as
described by Kuhn. Such an enterprise is not only ill-conceived and non-
existent; its defence is also incompatible with a humanitarian outlook.

CONSOLATIONS FOR THE SPECIALIST 2iI

8. AN ALTERNATIVE: THE LAKATOS MODEL OF SCIENTIFIC CHANGE

Let me now present in its entirety the picture of science which I think
should replace Kuhn’s account.

This picture is the synthesis of the following two discoveries. First, it
contains Popper’s discovery that science is advanced by a critical discussion
of alternative views. Secondly, it contains Kuhn’s discovery of the function
of tenacity which he has expressed, mistakenly I think, by postulating
tenacious periods. The synthesis consists in Lakatos’s assertion (which is
developed in his own comments on Kuhn) that proliferation and tenacity
do not belong to successive periods of the history of science, but are always
copresent.1

When speaking of ‘discoveries’ I do not mean to say that the ideas
mentioned are entirely new, or that they now appear in a new form. Quite
the contrary. Some of these ideas are as old as the hills. The idea that
knowledge can be advanced by a struggle of alternative views and that it
depends on proliferation was first put forth by the Presocratics (this has
been emphasized by Popper himself), and it was developed into a general
philosophy by Mill (especially in On Liberty). The idea that a struggle of
alternatives is decisive for science, too, was introduced by Mach (Erkenntnis
und Irrtum) and Boltzmann (see his Populaerwissenschaftliche Vorlesungen),
mainly under the impact of Darwinism. The need for tenacity was
emphasized by those dialectical materialists who objected to extreme
‘idealistic’ flights of fancy. And the synthesis, finally, is the very essence
of dialectical materialism in the form in which it appears in the writings
of Engels, Lenin, and Trotsky. Little of this is known to the ‘analytic’ or
‘empiricist’ philosophers of today who are still very much under the
influence of the Vienna Circle. Considering this narrow, though quite
‘modern’ context we may therefore speak of genuine though quite belated,
‘discoveries’.

According to Kuhn mature science is a succession of normal periods and
of revolutions. Normal periods are monistic; scientists try to solve puzzles
resulting from the attempt to see the world in terms of a single paradigm.
Revolutions are pluralistic until a new paradigm emerges that gains sufficient
support to serve as the basis for a new normal period.

This account leaves unanswered the problem how the transition from a
normal period to a revolution is brought about. In section 6 we indicated

t Lakatos’s analysis, I think, can be further improved by abandoning the distinction
between theories and research programmes (cf. above, p. 203, footnote 2) and by allowing
for incommensurability (jumps from quantity to quality in the Janguage of dialectical
materialism). Improved in this way it would be a truly dialectical account of the develop-
ment of our knowledge.

212 PAUL FEYERABEND

how the transition could be achieved in a reasonable manner: one com-
pares the central paradigm with alternative theories. Professor Kuhn seems
to be of the same opinion. Moreover he points out that this is what actually
happens. Proliferation sets in already before a revolution and is instrumental
in bringing it about. But this means that the original account is faulty.
Proliferation does not start with a revolution; it precedes it. A little imagina-
tion and a little more historical research then shows that proliferation not
only immediately precedes revolutions, but that it is there all the time.
Science as we know it is not a temporal succession of normal periods and
of periods of proliferation; it is their juxtaposition.

Seen in this way the transition from pre-science to science does not
replace the uninhibited proliferation and the universal criticism of the for-
mer by the puzzle-solving tradition of a normal science. It supplements it
by this activity or, to express it even better, mature science unites two very
different traditions which are often separate, the tradition of a pluralistic
philosophical criticism and a more practical (and less humanitarian—see
section 8) tradition which explores the potentialities of a given material
(of a theory; of a piece of matter) without being deterred by the difficulties
that might arise and without regard to alternative ways of thinking (and
acting), We have learned from Professor Popper that the first tradition is
closely connected with the cosmology of the Presocratics. The second tradi-
tion is best exemplified by the attitude of the members of a closed society
towards their basic myth. Kuhn has conjectured that mature science
consists in the succession of these two different patterns of thought and
action. He is right in so far as he has noticed the normal, or conservative,
or anti-humanitarian element. This is a genuine discovery. He ir wrong as
he has misrepresented the relation of this element to the more philoso-
phical (i.e. critical) procedures. I suggest in accordance with Lakatos’s
model that the correct relation is one of simultaneity and interaction. I shall
therefore speak of the normal component and the philosophical component
of science and not of the normal period and the period of revolution.

It seems to me that such an account overcomes many difficulties, both
logical and factual, which make Kuhn’s point of view so fascinating but at
the same time so unsatisfactory. In considering it one should not be

1 To take but one example, Kuhn writes (this volume, p. 6) that ‘it is for the normal, not
the extraordinary practice of science that professionals are trained; if they are nevertheless
eminently successful in displacing and replacing the theories on which normal science
depends, that is an oddity which must be explained’. It is certainly an oddity in Kuhn’s
account. In our account we only need to draw attention to the fact that revolutions are
mostly made by members of the philosophical component who, while aware of the normal
practice, are also able to think in a different way (in the case of Einstein the self-professed
ability to escape from the normal training was essential for his freedom of thought and for
his discoveries).

CONSOLATIONS FOR THE SPECIALIST 213

misled by the fact that the normal component almost always outweighs its
philosophical part. For what we are investigating is not the size of a certain
element of science, but its function (a single man can revolutionize an
epoch). Nor must we be overly impressed by the fact that most scientists
would regard the ‘philosophical’ component as lying outside science proper
and that they could support this attitude by pointing to their own lack of
philosophical acumen. For it is not they who carry out fundamental
improvement but those who further the active interaction of the normal and
the philosophical component (this interaction consists almost always in the
criticism of what is well entrenched and unphilosophical by what is peri-
pheral and philosophical). Now, granting all this, why is it that there seems
to exist a definite fluctuation in the state of science? If science consists of
the constant interaction of a normal and a philosophical part; if it is this
interaction which advances it; then why do the revolutionary elements
become visible only on such rare occasions? Is not this simple historical fact
sufficient to support Kuhn’s account over mine? Is it not typical philo-
sophical sophistry to deny what is such an obvious historical fact?

I think that the answer to this question is obvious. The normal com-
ponent is large and well entrenched. Hence, a change of the normal com-
ponent is very noticeable. So is the resistance of the normal component
to change. This resistance becomes especially strong and noticeable in
periods where a change seems to be imminent. It is directed against the
philosophical component and brings it into public consciousness. The
younger generation, always eager for new things, seizes upon the new
material and studies it avidly. Journalists, always on the lookout for head-
lines—the more absurd, the better—publicize the new discoveries (which
are those elements of the philosophical component which most radically
disagree with the current views while still possessing some plausibility and
perhaps even some factual support). These are some reasons for the
differences which we perceive. I do not think that one should look for
anything more profound.

Now as regards the change of the normal component itself there is no
reason to expect that it will follow a clearly recognizable and logical pattern.
Kuhn like other philosophers before him (I am here mainly thinking of
Hegel) assumes that a tremendous historical change must exhibit a logic
of its own and that the change of an idea must be reasonable in the sense
that there exists a link between the fact of change and the content of the
idea changing. This is a plausible assumption as long as one is dealing with
reasonable people: changes in the philosophical component most likely can
be explained as the result of clear and unambiguous arguments. But to
assume that people who habitually resist change; who frown at any criticism

214 PAUL FEYERABEND

of things dear to them; and whose highest aim is to solve puzzles on a
basis that is neither known nor understood; to assume that such people will
change their allegiance in a reasonable fashion is carrying optimism and
the quest for rationality too far. The normal elements, i.e. those elements
which have the support of the majority, may change because the younger
generation cannot be bothered to follow their elders; or because some public
figure has changed his mind; or because some influential member of the
establishment has died and has failed (perhaps because of his suspicious
nature) to leave behind a strong and influential school, or because a power-
ful and non-scientific institution pushes thought in a definite direction.*
Revolutions, then, are the outward manifestation of a change of the normal
component that cannot be accounted for in any reasonable fashion. They
are substance for anecdotes though they magnify and make visible the
more rational elements of science, thus teaching us what science could be
if there were more reasonable people around.

Q. THE ROLE OF REASON IN SCIENCE

(1) So far I have criticized Kuhn from a point of view which is almost
identical with that of Lakatos. (There are some slight differences, such as
my reluctance to separate theories and research programmes,? but they
will be disregarded. When speaking of ‘theories’ I always mean theories
and/or research programmes.) ] now want to defend Kuhn against Lakatos.
More specifically, I want to argue that science both is, and should be,
more irrational than Lakatos and Feyerabend, (the Popperian, author of

1 It is plausible to assume that one of the causes for the transition to mature science with
its various ‘quasi~independent’ traditions is to be sought in the decree of the Roman
Catholic Church against the Copernican point of view. “This must be taken into account
by those who try to explain the special development of the many individual sciences and the
absence of a conscious and secure philosophical background by regarding it as a peculiarity
of seventeenth-century Italian culture. ... Such an interpretation assumes... that the con-
demnation of Galileo was but an external pressure which could not possibly have influenced
the development of spiritual matters, However the Roman Judgement was regarded as a
restriction of consciousness that could be broken only on pain of life and salvation. ...
The development of individual disciplines was allowed. Nobody was prevented from search-
ing the heavens, from exploring physical phenomena, from thinking mathematically ...
and from furthering the material culture by such a pursuit. Priests and religious orders,
even the Jesuits who were responsible for Galileo’s fate, diligently pursued these restricted
tasks. But individual conscience as well as the omnipresent ‘directeurs de conscience’,
the officials, the schools, the churches, the state watched carefully this simple fight for
knowledge in order that no one might dare to use its results for philosophical speculation’.
(Leonardo Olschki [1927], p. 400). This is how ‘mature science’ came into being, at least in
the Roman countries. Cf. also chapter IX of Wohlwill’s [1926] where the development
after Galileo’s death is sketched in some detail.

2 Cf. above, p. 203, footnote 2.

CONSOLATIONS FOR THE SPECIALIST 215

the preceding sections of this paper and of ‘Problems of Empiricism’) are
prepared to admit.1

This transition from criticism to defence does not mean that I have
changed my mind. Nor can it be completely explained by my cynicism
vis-a-vis the business of philosophy of science. It is rather connected with
the nature of science itself, with its complexity, with the fact that it has
different aspects, that it cannot be readily separated from the remainder of
history, that it has always utilized and continues to utilize every talent and
every folly of man. Contrary arguments bring out the different features it
contains, they challenge us to make a decision, they challenge us to either
accept this many-faced monster and be devoured by it, or else to change it in
accordance with our wishes. Let us now see what can be said against the
Lakatos model of scientific growth.

(2) Naive falsificationism judges (i.e. accepts, or condemns) a theory as
soon as it is introduced into the discussion. Lakatos gives a theory time,
he permits it to develop, he permits it to show its hidden strength, and he
judges it only ‘in the long run’. The ‘critical standards’ he employs pro-
vide for an interval of hesitation. They are applied ‘with hindsight’.? They
are applied after the occurrence of either ‘progressive’ or of ‘degenerating’
problem shifts.

Now it is easy to see that standards of this kind have practical force only
if they are combined with a time limit (what looks like a degenerating prob-
lem shift may be the beginning of a much longer period of advance). But
introduce the time limit and the argument against naive falsificationism
reappears with only a minor modification (if you are permitted to wait, why
not wait a little longer?) Thus the standards which Lakatos wants to
defend are either vacuous—one does not know when to apply them—or
they can be criticized on grounds very similar to those which led to them
in the first place.

In these circumstances one can do one of the following two things. One
can stop appealing to permanent standards which remain in force through-
out history and govern every single period of scientific development and
every transition from one period to another. Or one can retain such stan-
dards as a verbal ornament, as a memorial to happier times when it was still
thought possible to run a complex and often catastrophic business like
science by following a few simple and ‘rational’ rules. It seems that Lakatos
wants to choose the second alternative.

1 The indices are intended as an ironical criticism of Lakatos [19686] where the practice
of splitting a guy into three was first introduced. (Also cf. this volume, p. 181.) This practice
has created a lot of confusion and has slowed down philosophers in their attempt to find
the weak spots of critical rationalism.

2 This volume, pp. 134, 158, and 173.

216 PAUL FEYERABEND

(3) Choosing the second alternative means abandoning permanent
standards in fact though retaining them in words. In fact, Lakatos’s position
now seems to be identical with the position of Popper as summarized in a
(because self-destructive) marvellous addendum of the fourth edition of
the Open Society.1 According to Popper we do not ‘need any . . . definite
frame of reference for our criticism’, we may revise even the most funda-
mental rules and drop the most fundamental demands if the need for a
different measure of excellence should arise.? Is such a position irrational?
Does it imply that science is irrational? Yes and no. Yes—because there no
longer exists a single set of rules that will guide us through all the twists
and turns of the history of thought (science), either as participants, or as
historians who want to reconstruct its course. One can of course force
history into such a pattern, but the results will always be poorer and much
less interesting than were the actual events. No—because each particular
episode is rational in the sense that some of its features can be ex-
plained in terms of reasons which were either accepted at the same time
as its occurrence, or invented in the course of its development. Yes—
because even these logical reasons which change from age to age are never
sufficient to explain all the important features of a particular episode. We
must add accidents, prejudices, material conditions (such as the existence
of a particular type of glass in one country and not in another), the vicis-
situdes of married life, oversight, superficiality, pride, and many other
things in order to get a complete picture. No—because transported into the
climate of the period under consideration and endowed with a lively and
curious intelligence we might have had still more to say, we might have
tried to overcome accidents, and to ‘rationalize’ even the most whimsical
sequence of events. But—and now we come to a decisive point—how is the
transition from certain standards to other standards to be achieved? More
especially, what happens to our standards (as opposed to our theories)
during a period of revolution? Are they changed in the Popperian manner,
by a critical discussion of alternatives, or are there processes which defy a
rational analysis? This is one of the questions raised by Kuhn. Let us see
what answer we can give to it!

(4) That standards are not always adopted on the basis of argument has
been emphasized by Popper himself. Children, he says, ‘learn to imitate
others .. . and so learn to look upon standards of behaviour as if they con-
sisted of fixed, ‘‘given” rules . .. and such things as sympathy and imagi-
nation may play an important role in this development’.* Similar con-
siderations apply to those grownups who want to continue learning and

1 Popper [1961], p. 388. 2 Loe. cit, p. 390.
® Lor. cit. p 390.

CONSOLATIONS FOR THE SPECIALIST 217

who are intent on expanding both their knowledge and their sensibility.
We certainly cannot assume that what is possible in the case of children—
to slide, on the smallest provocation, into entirely new reaction patterns—
should be beyond the reach of adults and inaccessible to one of the most
outstanding adult activities, science. Moreover, it is likely that catastrophic
changes, frequent disappointment of expectations, crises in the develop-
ment of our knowledge will change and, perhaps, multiply reaction patterns
(including patterns of argumentation) just as an ecological crisis multiplies
mutations. This may be an entirely natural process, like growing in size,
and the only function of rational discourse may consist in increasing the
mental tension that precedes and causes the behavioural outburst. Now—is
this not exactly the kind of change we may expect at periods of scientific
revolution? Does it not restrict the effectiveness of arguments (except as a
causative agent leading to developments very different from what is de-
manded by their content)? Does not the occurrence of such a change show
that science which, after all, is part of the evolution of man is not entirely
rational and cannot be entirely rational? For if there are events, not nec-
essarily arguments which cause us to adopt new standards, will it then not
be up to the defenders of the status quo to provide, not just arguments,
but also contrary causes? And if the old forms of argumentation turn out to
be too weak a contrary cause, must they then not either give up, or resort
to stronger and more ‘irrational’ means? (It is very difficult, and perhaps
entirely impossible, to combat the effects of brainwashing by argument.)
Even the most puritanical rationalist will then be forced to leave argument
and to use, say, propaganda not because some of his arguments have
ceased to be valid, but because the psychological conditions which enable
him to effectively argue in this manner and thereby to influence others have
disappeared. And what is the use of an argument that leaves people
unmoved?

(5) Considering questions such as these a Popperian will reply that new
standards may indeed be discovered, invented, accepted, imparted upon
others in a very irrational manner, but that there always remains the possi-
bility to criticize them after they have been adopted and that it is this
possibility which keeps our knowledge rational. ‘What, then, are we to
trust?’ asks Popper after a survey of possible sources for standards. ‘What
are we to accept? The answer is: whatever we accept we should trust only
tentatively, always remembering that we are in possession, at best, of partial
truth (or rightness), and that we are bound to make at least some mistake
or misjudgement somewhere—not only with respect to facts but also
with respect to the adopted standards; secondly, we should trust (even

1 Loe. cit. p. 391.
8

218 PAUL FEYERABEND

tentatively) our intuition only if it has been arrived at as the result of many
attempts to use our imagination; of many mistakes, of many tests, of many
doubts, and of searching criticism.’

Now this reference to tests and to criticism which is supposed to guarantee
the rationality of science and, perhaps, of our entire life may be either to
well defined procedures without which a criticism or test cannot be said to
have taken place, or it may be purely abstract so that it is left to us to fill it
now with this, and now with that concrete content. The first case has just
been discussed. In the second case we have but a verbal ornament, just as
Lakatos’s defence of his own ‘objective standards’ turned out to be a
verbal ornament. The questions of section 4 remain unanswered in either
case.

(6) In a way even this situation has been described by Popper who says
that ‘rationalism is necessarily far from comprehensive or self-contained’.*
But the question raised by Kuhn is not whether there are limits to our
reason; the question is where these limits are situated. Are they outside the
sciences so that science itself remains entirely rational, or are irrational
changes an essential part of even the most rational enterprise that has been
invented by man? Does the historical phenomenon ‘science’ contain in-
gredients which defy a rational analysis? Can the abstract aim to come
closer to the truth be reached in an entirely rational manner, or is it per-
haps inaccessible to those who decide to rely on argument only? These are
the problems to which we must now address ourselves.

(7) Considering these further problems Popper and Lakatos reject
‘mob psychology’? and assert the rational character of all science. Accord-
ing to Popper it is possible to arrive at a judgement as to which of two
theories is closer to the truth, even if the theories should be separated by a
catastrophic upheaval such as a scientific revolution. (A theory T is closer
to the truth than another theory, 7”, if the class of the true consequences of
T’, the so-called truth content of 7’, exceeds the class of true consequences
of T without an increase in the falsity content.) According to Lakatos the
apparently unreasonable features of science occur only in the material
world and in the world of (psychological) thought; they are absent from
the ‘world of ideas, [from] Plato’s and Popper’s “third world” ’.3 It is in this
third world that the growth of knowledge takes place and that a rational
judgement of all aspects of science becomes possible. It must be pointed
out, however, that the scientist is unfortunately dealing with the world of
matter and of (psychological) thought also and that the rules which create
order in the third world may be entirely inappropriate for creating order

1 Popper [1945], chapter 24. 2 This volume, p. 178.
8 This volume, p. 180.

CONSOLATIONS FOR THE SPECIALIST 219

in the brains of living human beings (unless these brains and their struc-
tural features are put into the third world, a point that does not become
clear from Popper’s account). The numerous deviations from the straight
path of rationality which we observe in actual science may well be necessary
if we want to achieve progress with the brittle and unreliable material
(instruments; brains; etc.) at our disposal.

However there is no need to pursue this objection further. There is
no need to argue that real science may differ from its third world image in
precisely those respects which make progress possible.? For the Popperian
model of an approach to the truth breaks down even if we confine our-
selves to ideas entirely. It breaks down because there are incommensurable
theories.

(8) With the discussion of incommensurability, I come to a point of
Kuhn’s philosophy which I wholeheartedly accept. I am referring to his
assertion that succeeding paradigms can be evaluated only with difficulty
and that they may be altogether incomparable, at least as far as the more
familiar standards of comparison are concerned (they may be readily
comparable in other respects). I do not know who of us was the first to use
the term ‘incommensurable’ in the sense that is at issue here. It occurs in
Kuhn’s ‘Structure of Scientific Revolutions’ and in my essay ‘Explanation,
Reduction, and Empiricism’ both of which appeared in 1962. I still re-
member marvelling at the pre-established harmony that made us not only
defend similar ideas but use exactly the same words for expressing them.
The coincidence is of course far from mysterious. I had read earlier drafts
of Kuhn’s book and had discussed their content with Kuhn. In these dis-
cussions we both agreed that new theories, while often better and more
detailed than their predecessors were not always rich enough to deal with
all the problems to which the predecessor had given a definite and precise
answer. The growth of knowledge or, more specifically, the replacement
of one comprehensive theory by another involves losses as well as gains.
Kuhn was fond of comparing the scientific world view of the seventeenth
century with the Aristotelian philosophy, while I used more recent ex-
amples such as the theory of relativity and the quantum theory. We also
saw that it might be extremely difficult to compare successive theories in

1 | am here referring to Popper [1968a] and Popper [19688]. In the first paper birdnests
are assigned to the “Third World’ (p. 341) and an interaction is assumed between them and
the remaining worlds. They are assigned to the Third World because of their function. But
then stones and rivers can be found in this third world, too, for a bird may sit on a stone,
or take a bath in a river. As a matter of fact, everything that is noticed by some organism
(and therefore plays a role in his Umwelt) will be found in the third world which will there-
fore contain the whole material world and all the mistakes mankind has made. It will
also contain ‘mob psychology’.

? Cf, my [1969].

220 PAUL FEYERABEND

the usual manner, that is, by an examination of consequence classes. The
accepted scheme is as follows (Fig. 1): T is superseded by T’. T’ explains
why T fails where it does (in F); it also explains why T has been at least
partly successful (in S); and makes additional predictions, (A). Now if
this scheme is to work then there must be statements which follow (with,
or without the help of definitions and/or correlation hypotheses) both from
T and from T’. But there are cases which invite a comparative judgement
without satisfying the conditions just stated. The relation between such
theories is as shown in Fig. 2.1 A judgement involving a comparison of
content classes is now clearly impossible. For example, 7’ cannot be said
to be either closer to, or farther from, the truth, than 7.

’
’

y T T
/\ \
LA gn SS ~- /\

Fig. 1 Fig. 2

(9) Asan example of two incommensurable theories let us briefly discuss
classical celestial mechanics (CM) and the special theory of relativity (SR).
To start with one should emphasize that the question ‘are CM and SR
incommensurable?’ is not a complete question. Theories can be inter-
preted in different ways. They will be commensurable in some interpre-
tations, incomparable in others. Instrumentalism, for example, makes
commensurable all those theories which are related to the same observa-
tion language and are interpreted on its basis. A realist, on the other hand,
wants to give a unified account, both of observable and of unobservable
matters, and he will use the most abstract terms of whatever theory he is
contemplating for that purpose. This is an entirely natural procedure. SR,
so one would be inclined to say, does not just invite us to rethink unobserved
length, mass, duration; it would seem to entail the relational character of
all lengths, masses, durations, whether observed or unobserved, observ-
able or unobservable. Now extending the concepts of a new theory T to all
its consequences, observational reports included, may change the interpre-
tation of these consequences to such an extent that they disappear from the
consequence classes of earlier theories. These earlier theories will then all

1'The area below J’ should be imagined as lying either in front of the area below T,
or behind it, so that there is no overlap.

CONSOLATIONS FOR THE SPECIALIST 221

become incommensurable with 7. The relation between SR and CM is
a case in point. The concept of length as used in SR and the concept of
length as presupposed in CM are different concepts. Both are relational
concepts, and very complex relational concepts at that (just consider
determination of length in terms of the wave length of a specified spectral
line). But relativistic length (or relativistic shape) involves an element that
is absent from the classical concept and is in principle excluded from it.!
It involves the relative velocity of the object concerned in some reference
system. It is of course true that the relativistic scheme very often gives us
numbers which are practically identical with the numbers we get from
CM—but this does not make the concepts more similar. Even the case
c— co (or vo) which gives strictly identical predictions cannot be used as
an argument for showing that the concepts must coincide at least in this
case: different magnitudes based on different concepts may give identical

1 It is possible to base space time frames on this new element only and to avoid contamina-
tion by earlier modes of thought. All one has to do is to replace distances by light-times and
to treat time intervals in the relativistic fashion, for example, by using the &-calculus.
(Cf. chapter II of Synge [1964]. For the k-calculus, cf. Bondi [1967], pp. 29 ff., as well as
Bohm [1965], chapter xxvi.) The resulting concepts (of distance, velocity, time, etc.)
are a necessary part of relativity in the sense that all further ideas such as the idea of length
as defined by the transport of rigid rods must be changed and adapted to them. ‘They
therefore suffice for explaining relativity.

Marzke and Wheeler [1963] have given a detailed account of the way in which the theory
of relativity can be freed from external ingredients. They adopt the principle, ascribed by
them to Bohr and Rosenfeld, ‘that every proper theory should provide in and by itself its
own means for defining the quantities with which it deals, According to this principle
classical general relativity should admit to calibrations of space and time that are altogether
free of any reference to the quantum of action [for atomic clocks, or minimal distances]’ or to
‘rigid rods’ as described by, say, the non relativistic theory of elasticity (p. 48). They proceed
to construct clocks and meters which use the properties of light and of inertial particle
trajectories only (pp. 53-6). Equality of distances measured by such clocks and meters is
intransitive in a classical universe, transitive in a relativistic universe. The results of distance
measurements of this kind are invariant to translations in a relativistic universe, not so
invariant in a classical universe. Two different events are always separated by a finite
distance in a relativistic universe, they are not always so separated in a classical universe.
The unity of measurement in the relativistic universe is the interval between the two
effective equinoxes of 1900 and it can be compared with any interval (spatial or temporal)
in an invariant way. No such comparison is possible in the classical case (p. 62). “The
number 3.10° never shows itself. The importance of lightrays and the lightcone in the
intrinsic geometry of physics comes more directly to the surface. The true function of the
speed of light is no longer confused with the trivial task of relating two separate units of
interval, the meter and the second, of purely historical and accidental origin’ (p. 56).
General relativity theory, then, can be shown to ‘provide its own means of defining intervals
of space and time’ (p. 62) and the intervals so defined are incommensurable with classical
intervals. ;

Space forbids to argue this interesting case in detail but it is hoped that those who are
turned on by the problem of incommensurability will use Marzke and Wheeler as a basis
fer concrete discussion.

222 PAUL FEYERABEND

values on their respective scales without ceasing to be different magni-
tudes (the same remark applies to the attempt to identify classical mass
with relative rest mass).1 This conceptual disparity, if taken seriously,
infects even the most ‘ordinary’ situations: the relativistic concept of a
certain shape, such as a table, or of a certain temporal sequence, such as
my saying ‘yes’, will differ from the corresponding classical concept also.
It is therefore vain to expect that sufficiently long derivations may eventually
return us to the older ideas. The consequence classes of SR and CM are
related as in Fig. 2. A comparison of content and a judgement of verisi-
militude cannot be made.®

(10) In what follows I shall discuss a few objections which have been
raised, not against this particular analysis of the relation between SR and
CM, but against the very possibility, or desirability of incommensurable
theories (almost all objections against incommensurability are of this
general kind). They express methodological ideas which we must criticize
if we want to increase our freedom vis-d-vis the sciences.

One of the most popular objections proceeds from the version of realism
that I just described in (9). ‘A realist’, we said, ‘wants to give a unified
account, both of observable and of unobservable matters, and he will use
the most abstract terms of whatever theory he is contemplating for that
purpose’. He will use such terms in order to either give meaning to observa-
tion sentences, or else to replace their customary interpretation (for ex-
ample, he will use the ideas of SR in order to replace the customary CM-
interpretation of everyday statements about shapes, temporal sequences,
and so on). As against this it is pointed out that theoretical terms receive
their interpretation by being connected either with a pre-existing observa-
tion language, or with another theory that has already been connected with
such an observation language and that they are devoid of content without
such a connection. Thus Carnap asserts* that ‘there is no independent
interpretation for Ly [the language in terms of which a certain theory, or a
certain world view, is formulated]. The system T [consisting of the axioms
of the theory and the rules of derivation] is itself an uninterpreted postulate

1 For this point and further arguments, cf. Eddington [1924], p. 33.

2 "This takes care of an objection which John Watkins has raised on various occasions.

3 For further details, especially concerning the concept of mass, the function of ‘bridge
laws’ or ‘correspondence rules’, and the two-language model, cf. section IV of my [1965}}.
It is clear that, given the situation described in the text, we cannot derive classical mechanics
from relativity, not even approximately (for example, we cannot derive the classical law
of mass conservation from a corresponding relativistic law). The possibility to connect the
formulae of the two disciplines in a manner that might satisfy a pure mathematician (or an
instrumentalist) is however not excluded. For an analogous situation in the case of quantum
mechanics cf. section 3 of my [1968-9]. Cf. also section z of the same article for more general
considerations. * Cf. Carnap [1956], p. 47.

CONSOLATIONS FOR THE SPECIALIST 223

system. [Its] terms obtain only an indirect and incomplete interpretation by
the fact that some of them are connected by the [correspondence rules] C with
observational terms’. Now, if theoretical terms have no ‘independent inter-
pretation’ then they cannot be used for correcting the interpretation of the
observation statements which is the one and only source of their meaning.
It follows that realism as described by us is an impossible doctrine.

The guiding idea behind this objection is that new and abstract languages
cannot be introduced in a direct way but must be first connected with an
already existing, and presumably stable, observational idiom.!

This guiding idea is refuted at once by pointing to the way in which
children learn to speak and in which anthropologists and linguists learn
the unknown language of a newly discovered tribe.

The first example is instructive for other reasons also, for incommensur-
ability plays an important role in the early months of human development.
As has been suggested by Piaget and his school,? the child’s perception
develops through various stages before it reaches its relatively stable
adult form. In one stage objects seem to behave very much like after-
images*—and they are treated as such: the child follows the object with his
eyes until it disappears and he does not make the slightest attempt to
recover it even if this would require a minimal physical (or intellectual)
effort, an effort moreover, that is already within the child’s reach. There is
not even a tendency to search—and this is quite appropriate, ‘conceptually’
speaking. For it would indeed be nonsensical to ‘look for’ an afterimage. Its
‘concept’ does not provide for such an operation.

The arrival of the concept, and of the perceptual image, of material
objects changes the situation quite dramatically. There occurs a drastic
reorientation of behavioural patterns and, so one may conjecture, of thought.
Afterimages or things somewhat like them still exist, but they are now
difficult to find and must be discovered by special methods (the earlier
visual world therefore literally disappears). Such methods proceed from a
new conceptual scheme (afterimages occur in humans, not in the outer
physical world, and are tied to them) and cannot lead back to the exact

1 An even more conservative principle is sometimes used when discussing the possibility
of languages with a logic different from our own, Thus Stroud, in his [1968], discussing,
and not just stating the principle, says that ‘any allegedly new possibility must be capable
of being fitted into, or understood in terms of, our present conceptual or linguistic apparatus’
from which it follows (172) that ‘any “alternative” is either something we already under-
stand and can make sense of, or it is no alternative at all’. What is overlooked is that an initi-
ally ununderstood alternative may be /earned in the way in which one learns a new and un-
familiar language, not by translation, but by living with the members of the community
where the language is spoken.

2 As an example the reader is invited to consult Piaget (1954].

5 Piaget [1954], pp. 5 ff.

224 PAUL FEYERABEND

phenomena of the previous stage (these phenomena should therefore be
called by a different name, such as ‘pseudo-afterimages’). Neither after-
images, nor pseudo-afterimages are given a special position in the new
world. For example, they are not treated as evidence on which the new
notion of a material object is supposed to rest. Nor can they be used to
explain this notion: afterimages arise together with it and are absent from
the mind of those who do not yet recognize material objects; and pseudo-
afterimages disappear as soon as such recognition takes place. It is to be
admitted that every stage possesses a kind of observational ‘basis’ to which
one pays special attention and from which one receives a multitude of
suggestions. However this basis (z) changes from stage to stage; and (2) it is
part of the conceptual apparatus of a given stage, noi its one and only
source of interpretation.

Considering developments such as these we may suspect that the family
of concepts centering upon ‘material object’ and the family of concepts
centering upon ‘pseudo-afterimages’ are incommensurable in precisely the
sense that is at issue here. Is it reasonable to expect that conceptual changes
of this kind occur only in childhood? Should we welcome the fact—if it is a
fact—that an adult is stuck with a stable perceptual world and an accom-
panying stable conceptual system which he can modify in many ways but
whose general outlines have forever become immobilized? Or is it not
more realistic to assume that fundamental changes, entailing incommen-
surability, are still possible, and that they should be encouraged lest we
remain forever excluded from what might be a higher stage of knowledge
and of consciousness? Besides, the question of the mobility of the adult
stage is at any rate an empirical question which must be attacked by
research and cannot be settled by methodological fiat. An attempt to break
through the boundaries of a given conceptual system and to escape the
range of ‘Popperian spectacles”! is an essential part of such research.”

(11) Looking now at the second element of the refutation—anthro-
pological field work—we see that what is anathema here (and for very good

1 Cf, Lakatos’s paper, this volume, p. 179, footnote 1.

2 For the condition of research formulated in the last sentence, cf. section 8 of my
[196sa]. For the role of observation cf. section 7 of the same article. For the application of
Piaget’s work to physics and, more especially, to the theory of relativity, cf. the appendix of
Bohm [1965]. Bohm and Schumacher have also carried out an analysis of the different
informal structures which underlie our theories. One of the main results of their work is
that Bohr and Einstein argued from incommensurable points of view. Seen in this way the
case of Einstein, Podolski and Rosen cannot refute the Copenhagen interpretation, and it
cannot be refuted by it. The situation is rather that we have two theories, one permitting us
to formulate the Einstein—Podolski-Rosen thought-experiment, the other not providing
the machinery necessary for such a formulation so that we must find independent means of
deciding which one to adopt. For further comments on this problem, cf. section 9 of my
[1968-9].

CONSOLATIONS FOR THE SPECIALIST 225

reasons) is still a fundamental principle for the contemporary representa-
tives of the philosophy of the Vienna Circle. According to Carnap, Feig!,
Nagel, and others the terms of a theory receive their interpretation, in an
indirect fashion, by being related to a different conceptual system which is
either an older theory, or an observation language. Older theories, or
observation languages are adopted not because of their theoretical excellence
(they cannot possibly be: the older theories are usually refuted). They are
adopted because they are ‘used by a certain language community as a
means of communication’.? According to this method, the phrase ‘having
much larger relativistic mass than...’ is partially interpreted by first
connecting it with some prerelativistic terms (classical terms; common-
sense terms) which are ‘commonly understood’ (presumably as the result
of previous teaching in connection with crude weighing methods). This
is even worse than the once quite popular demand to clarify doubtful
points by translating them into Latin. For while Latin was chosen because
of its precision and clarity and also because it was conceptually richer than
the slowly evolving vulgar idioms, the choice of an observation language or
of an older theory as a basis for interpretation is due to the fact that they
are ‘antecedently understood’, it is due to their popularity. Besides, if
prerelativistic terms which are pretty far removed from reality—especially
in view of the fact that they come from an incorrect theory—can be taught
ostensively, for example, with the help of crude weighing methods (and we
must assume that they can be so taught, or the whole scheme collapses)
then why should we not introduce the relativistic terms directly, and
without assistance from the terms of some other idiom? Finally, it is but
plain commonsense that the teaching, or the learning, of new and unknown
languages must not be contaminated by external material. Linguists
remind us that a perfect translation is never possible, even if we use com-
plex contextual definitions. This is one of the reasons for the importance
of field work where new languages are learned from scratch and for the
rejection, as inadequate, of any account that relies on (complete, or partial)
translation. Yet just what is anathema in linguistics is now taken for granted
by logical empiricists, a mythical ‘observation language’ replacing the English
of the translators. Let us commence field work in this domain also and let
us study the language of new theories not in the definition factories of the
double language model, but in the company of those metaphysicians, experi-
menters, theoreticians, playwrights, courtesans, who have constructed new
world views! This finishes our discussion of the guiding principle of the first
objection against realism and the possibility of incommensurable theories.

1 For what follows, cf. also my [1966].
® Carnap [1956], p. 40. Cf. also Hempel [1966], pp. 74 ff.

226 PAUL FEYERABEND

(12) Next I shall deal with a mixed bag of asides which have never been
presented in a systematic fashion and which can be disposed of in a few
words.

To start with, there is the suspicion that observations which are inter-
preted in terms of a new theory can no longer be used to refute that theory.
The suspicion is allayed by pointing out that the predictions of a theory
depend on its postulates, the associated grammatical rules as well as on
initial conditions, while the meaning of the primitive notions depends on the
postulates (and the associated grammatical rules) only: it is possible to
refute a theory by an experience that is entirely interpreted in its terms.

Another point that is often made is that there exist crucial experiments
which refute one or two allegedly incommensurable theories and confirm
the other, for example: the Michelson—Morley experiment, the variation
of the mass of elementary particles, the transversal Doppler effect refute
CM and confirm SR. The answer to this problem is not difficult either:
adopting the point of view of relativity we find that the experiments which
of course will now be described in relativistic terms, using the relativistic
notions of length, duration, speed, and so on,! are relevant to the theory and
we shall also find that they support the theory. Adopting CM (with, or
without an aether) we again find that the experiments (which are now
described in the very different terms of classical physics, roughly in the
manner in which Lorentz described them) are relevant, but we also find
that they undermine (the conjunction of classical electrodynamics and of)
CM. Why should it be necessary to possess terminology that allows us to
say that it is the same experiment which confirms one theory and refutes
the other? But did we not ourselves use such terminology? Well, for one
thing it should be easy, though somewhat laborious, to express what was
just said without asserting identity. Secondly, the identification is of course
not contrary to our thesis, for we are now not using the terms of either

relativity, or of classical physics, as is done in a test, but are referring to
them and their relation to the physical world. The language in which this
discourse is carried out can be classical, or relativistic, or ordinary. It is no
good insisting that scientists act as if the situation were much less compli-
cated. If they act that way, then they are either instrumentalists (see above,
section g) or mistaken: many scientists are nowadays interested in formulae
while we are discussing interpretations. It is also possible that being well
acquainted with both CM and SR they change back and forth between
these theories with such speed that they seem to remain within a single
domain of discourse.

(13) It is also said that in admitting incommensurability into science we

1 For examples of such descriptions cf. Synge [1964].

CONSOLATIONS FOR THE SPECIALIST 227

can no longer decide whether a new view explains what it is supposed to
explain or whether it does not wander off into different fields. For example,
we would not know whether a newly invented physical theory is still
dealing with problems of space and time or whether its author has not by
mistake made a biological assertion. But there is no need to possess such
knowledge. For once the fact of incommensurability has been admitted the
question which underlies the objection does not arise (conceptual progress
often makes it impossible to ask certain questions; thus we can no longer
ask for the absolute velocity of an object—at least as long as we take
relatively seriously). Yet is this not a serious loss for science? Not at all!
Progress was made by the very same ‘wandering off into different fields’
whose undecidability now so greatly exercises the critic: Aristotle saw the
world as a superorganism, that is, as a biological entity, while one essential
element of the new science of Descartes, Galileo, and of their followers in
medicine and in biology is its exclusively mechanistic outlook. Are such
developments to be forbidden? And if they are not, then what is left of the
complaint?

A closely connected objection starts from the notion of explanation, or
reduction, and emphasizes that this notion presupposes continuity of con~-
cepts (other notions could be used for starting exactly the same kind of
argument). Now to take our above example, relativity is supposed to ex-
plain the valid parts of classical physics, hence it cannot be incommensur-
able with it! The reply is again obvious. Why should the relativist be con-
cerned with the fate of classical mechanics except as part of a historical
exercise? There is only one task we can legitimately demand of a theory and
it is that it should give us a correct account of the world. What have the
principles of explanation got to do with this demand? Is it not reasonable
to assume that a point of view such as the point of view of classical mech-
anics that has been found wanting in various respects cannot have entirely
adequate concepts, and is it not equally reasonable to try replacing its
concepts by those of a more successful cosmology? Besides, why should the
notion of explanation be burdened by the demand for conceptual con-
tinuity? This notion has been found to be too narrow before (demand of
derivability) and it had to be widened so as to include partial and statistical
connections. Nothing prevents us from widening it still further to admit,
say, ‘explanation by equivocation’.

(14) Incommensurable theories, then, can be refuted by reference to
their own respective kinds of experience (in the absence of commensurable
alternatives these refutations are quite weak, however)! Their content
cannot be compared. Nor is it possible to make a judgement of vertsimilitude

1 For this point cf. section 1 of my [19654], as well as my [19658].

228 PAUL FEYERABEND

except within the confines of a particular theory. None of the methods
which Popper wants to use for rationalizing science can be applied and the
one that can be applied, refutation, is greatly reduced in strength. What
remains are aesthetic judgements, judgements of taste, and our own sub-
jective wishes. Does this mean that we are ending up in subjectivism? Does
this mean that science has become arbitrary, that it has become one
element of the general relativism which Popper wants to attack? Let us see.

To start with, it seems to me that an enterprise whose human character
can be seen by all is preferable to one that looks ‘objective’, and impervious
to human actions and wishes.! The sciences, after all, are our own creation,
including all the severe standards they seem to impose upon us. It is good
to be constantly reminded of this fact. It is good to be constantly reminded
of the fact that science as we know it today is not inescapable and that we
may construct a world in which it plays no role whatever (such a world, I
venture to suggest, would be more pleasant than the world we live in
today). What better reminder is there than the realization that the choice
between theories which are sufficiently general to provide us with a
comprehensive world view and which are empirically disconnected may
become a matter of taste? That the choice of our basic cosmology may
become a matter of taste?

Secondly, matters of taste are not completely beyond the reach of argu-
ment. Poems, for example, can be compared in grammar, sound structure,
imagery, rhythm, and can be evaluated on such a basis (cf. Ezra Pound on
progress in poetry).2 Even the most elusive mood can be analysed, and must
be analysed if the purpose is to present it in a manner that can either be
enjoyed, or that increases the emotional (cognitive, perceptual) inventory
of the reader. Every poet who is not completely irrational compares,
improves, argues until he finds the correct formulation of what he wants
to say.2 Would it not be marvellous if this process played a role in the
sciences also?

Finally, there are more pedestrian ways of explaining the same matter
which may be somewhat less repulsive to the ears of a professional phil-
osopher of science. We may consider the length of derivations leading from

1 For this problem of ‘alienation’ cf. Marx [1844a] and [18448].

® Popper has repeatedly asserted, both in his lectures, and in his writings that while
there is progress in the sciences there is no progress in the arts. He bases his assertion on
the belief that the content of succeeding theories can be compared and that a judgement
of verisimilitude can be made. The refutation of this belief eliminates an important differ-
ence (and perhaps the on/y important difference) between science and the arts and makes
it possible to speak of styles and preferences in the first, and of progress in the second.

3 Cf. Brecht [1964], p. 119. In my lectures on the theory of knowledge I usually present

and discuss the thesis that finding a new theory for given facts is like finding a new produc-
tion for a well-known play. For painting, cf. also Gombrich [1960].

CONSOLATIONS FOR THE SPECIALIST 229

the principles of a theory to its observation language, and we may also
draw attention to the number of approximations made in the course of the
derivation (all derivations must be standardized for this purpose so that an
unambiguous judgement of length can be made; this standardization con-
cerns the form of the derivation, it does not concern the content of the con-
cepts used). Smaller length and smaller number of approximations would
seem to be preferable. It is not easy to see how this requirement can be
made compatible with the demand for simplicity and generality which, so
it seems, would tend to increase both parameters. However that may be—
there are many ways open to us once the fact of incommensurability is
understood, and taken seriously.

(15) I started by pointing out that scientific method, as softened up by
Lakatos, is but an ornament which makes us forget that a position of
‘anything goes’ has in fact been adopted. I then considered the argument
that the method of problemshifts, while perhaps useless in the first world
might still give a correct account of what goes on in the third world and
that it might permit us to view the whole ‘third world’ through ‘Popperian
spectacles’. The reply was that there is trouble in the third world also and
that the attempt to judge cosmologies by their content may have to be given
up. Such a development, far from being undesirable, changes science from
a stern and demanding mistress into an attractive and yielding courtesan
who tries to anticipate every wish of her lover. Of course, it is up to us
to choose either a dragon or a pussy cat for our company. I do not think I
need to explain my own preferences.

REFERENCES

Bohm [1965]: The Special Theory of Relativity, 1965.

Bondi [1967]: Assumption and Myth in Physical Theory, 1967.

Brecht [1964]: ‘Uber das Zerpfliicken von Gedichten’, in Uber Lyrik, 1964.

Carnap [1956]: ‘The Methodological, Character of Theoretical Concepts’, in Feigl and
Scriven (eds.): Minnesota Studies in the Philosophy of Science, 1, pp. 38-76.

Eddington [1924]: The Mathematical Theory of Relativity, 1924.

Epstein [1967]: Varieties of Perceptual Learning, 1967.

Feyerabend [1962]: ‘Explanation, Reduction and Empiricism’, in Feigl-Maxwell (eds.):
Minnesota Studies in the Philosophy of Science, 3, pp. 28-97.

Feyerabend [19652]: ‘Reply to Criticism’, in Cohen and Wartofsky (eds.): Boston Studies
in the Philosophy of Science, 2, pp. 223-61.

Feyerabend [19655]: ‘Problems of Empiricism’, in Colodny (ed.): Beyond the Edge of
Certainty, pp. 145-260.

Feyerabend [1966]: Review of Nagel’s ‘Structure of Science’, The British Journal for the
Philosophy of Science, 17, pp. 237-49.

Feyerabend [1968-9]: ‘On a Recent.Critique of Complementarity’, Philosophy of Science,
35, PP. 309-31 and 36, pp. 82-105.

Feyerabend [1969]: ‘Problems of Empiricism, part 2’, in Colodny (ed.): The Nature and
Function of Scientifie Theory, 1969.

230 PAUL FEYERABEND

Feyerabend [1970a]: ‘Classical Empiricism’, in Butts (ed.): The Methodological Heritage
of Newton, 1970.

Feyerabend [1970b]: ‘Against Method’, Minnesota Studies in the Philosophy of Science, 4.

Gombrich [1960]: Art and Illusion, 1960.

Hempel [1966]: Philosophy of Natural Science, 1966.

Kuhn [19614]: “The Function of Dogma in Scientific Research’, in Crombie (ed.): Scientific
Change, 1963, pp. 347-69 and 386-95.

Kuhn [19615]: ‘Measurement in Modern Physical Science’, Isis, 52, pp. 161-93.

Kuhn [1962]: The Structure of Scientific Revolutions, 1962.

Lakatos [1963-4]: ‘Proofs and Refutations’, The British Journal for the Philosophy of
Science, 14, pp. 1-25, 120-39, 221-43 and 296-342.

Lakatos [19684]: ‘Changes in the Problem of Inductive Logic’, in Lakatos (ed.): The
Problem of Inductive Logic, pp. 315-417.

Lakatos [19685]: ‘Criticism and the Methodology of Scientific Research Programmes’, in
Proceedings of the Aristotelian Society, 69, pp. 149-86.

Marx [18444]: Nationalékonomie und Philosophie, 1932.

Marx [1844b]: ‘Zur Kritik der Hegelschen Rechtsphilosophie,’ Deutsch-Franzésische
Jahrbiicher, 1844.

Marzke and Wheeler [1963]: ‘Gravitation and Geometry I: the geometry of space-time and
geometrodynamical standard meter’, in Chiu and Hoffmann (eds.): Gravitation and
Relativity, pp. 40-64.

Newton [1672]: Letter to Pardies, 10.6.1672, in Turnbull (ed.): The Correspondence of
Isaac Newton, 1, 1959, pp. 163-71.

Olschki [1927]: Geschichte der neusprachlichen wissenschaftlichen Literatur, 3, Galilet und
seine Zeit, 1927.

Piaget [1954]: The Construction of Reality in the Child, 1954.

Popper [1945]: The Open Society and its Enemies, I-II, 1945.

Popper [1961]: ‘Fact, Standards, and Truth: a further criticism of relativism’, Addendum 1
in the fourth edition of Popper [1945], vol. II. pp. 369-96, 1962.

Popper [1968a]: ‘Epistemology without a Knowing Subject’, in Rootselaar-Staal (eds.):
Proceedings of the Third International Congress for Logic, Methodology and Philosophy
of Science, pp. 333-73.

Popper [19684]: ‘On the Theory of the Objective Mind’, in Proceedings of the XIV Inter-
national Congress of Philosophy, 1, pp. 25-53.

Putnam [1963]: ‘ ‘Degree of Confirmation” and Inductive Logic’, in Schilpp (ed.): The
Philosophy of Rudolf Carnap, pp. 761-83.

Reagan [1967]: ‘Basic and Applied Research: A Meaningful Distinction?’, Science, 155,
pp. 1383-86.

Stroud [1968]: ‘Conventionalism and the Indeterminacy of Translation’, Synthese, 18,
pp. 82-96.

Synge [1964]: ‘Introduction to General Relativity’, in de Witt and de Witt (eds.): Relativity,

Groups and Topology, 1964.
Wohlwill [1926]: Galileo und sein Kampf fiir die Kopernikanische Lehre, 2, 1926.

Reflections on my Critics'

THOMAS S. KUHN
Princeton University

1. Introduction.

2. Methodology: the role of history and sociology.
3. Normal Science: its nature and functions.

4. Normal Science: its retrieval from history.

5. Irrationality and Theory-Choice.

6. Incommensurability and Paradigms.

I. INTRODUCTION

It is now four years since Professor Watkins and I exchanged mutually
impenetrable views at the International Colloquium in the Philosophy of
Science held at Bedford College, London. Rereading our contributions
together with those that have since accreted to them, I am tempted to posit
the existence of two Thomas Kuhns. Kuhn, is the author of this essay and
of an earlier piece in this volume. He also published in 1962 a book called
The Structure of Scientific Revolutions, the one which he and Miss Master-
man discuss above. Kuhn, is the author of another book with the same
title. It is the one here cited repeatedly by Sir Karl Popper as well as by
Professors Feyerabend, Lakatos, Toulmin, and Watkins. ‘That both books
bear the same title cannot be altogether accidental, for the views they
present often overlap and are, in any case, expressed in the same words.
But their central concerns are, I conclude, usually very different. As re-
ported by his critics (his original has unfortunately been unavailable to
me), Kuhn, seems on occasion to make points that subvert essential
aspects of the position outlined by his namesake.

Lacking the wit to extend this introductory fantasy, I will instead
explain why I have embarked upon it. Much in this volume testifies to
what I described above as the gestalt-switch that divides readers of my
Scientific Revolutions into two groups. Together with that book, this
collection of essays therefore provides an extended example of what
I have elsewhere called partial or incomplete communication—the

1 Though my battle with a publication deadline allowed them almost no time for it, my
colleagues C. G. Hempel and R. E. Grandy both managed to read my first manuscript and
offer useful suggestions for its improvement, conceptual and stylistic. I am most grateful
to them, but they should not be blamed for my views.

231

232 THOMAS S. KUHN

talking-through-each-other that regularly characterizes discourse between
participants in incommensurable points of view.

Such communication breakdown is important and needs much study.
Unlike Paul Feyerabend (at least as I and others are reading him), I do
not believe that it is ever total or beyond recourse. Where he talks of in-
commensurability tout court, I have regularly spoken also of partial com-
munication, and I believe it can be improved upon to whatever extent
circumstances may demand and patience permit, a point to be elaborated
below. But neither do I believe, as Sir Karl does, that the sense in which
‘we are prisoners caught in the framework of our theories; our expecta-
tions; our past experiences; our language’ is merely ‘Pickwickian’. Nor do I
suppose that ‘we can break out of our framework at any time... [into]
a better and roomier one... [from which] we can at any moment break
out... again.’! If that possibility were routinely available, there ought to
be no very special difficulties about stepping into someone else’s framework
in order to evaluate it. My critics’ attempts to step into mine suggest, how-
ever, that changes of framework, of theory, of language, or of paradigm
pose deeper problems of both principle and practice than the preceding
quotations recognize. These problems are not simply those of ordinary
discourse, nor will they be resolved by quite the same techniques. If they
could be, or if changes of framework were normal, occurring at will and at
any moment, they would not be comparable, in Sir Karl’s phrase, to ‘the
culture clash[es] which [have] stimulated some of the greatest intellectual
revolutions.’”? The very possibility of that comparison is what makes them
so very important.

One especially interesting aspect of this volume is, then, that it provides
a developed example of a minor culture clash, of the severe communication
difficulties which characterize such clashes, and of the linguistic techniques
deployed in the attempt to end them. Read as an example, it could be an
object for study and analysis, providing concrete information concerning a
type of developmental episode about which we know very little. For some
readers, I suspect, the recurrent failure of these essays to intersect on
intellectual issues will provide this book’s greatest interest. Indeed, be-
cause those failures illustrate a phenomenon at the heart of my own point
of view, the book has that interest for me. I am, however, too much a par-
ticipant, too deeply involved, to provide the analysis which the breakdown
of communication warrants. Instead, though I remain convinced that their
fire is frequently misplaced and that it often obscures the deeper differences
between Sir Karl’s views and my own, I must here speak primarily to the
points raised by my present critics.

1 This volume, p. 56. 2 This volume, p. $7.

REFLECTIONS ON MY CRITICS 233

Those points, excepting for the moment the ones raised in Miss Master-
man’s stimulating paper, fall into three coherent categories, each of which
illustrates what I have just called the failure of our discussion to intersect
on issues. The first, for purposes of my discussion, is the perceived differ-
ence in our methods: logic versus history and social psychology; normative
versus descriptive. These, as I shall shortly try to show, are odd contrasts
with which to discriminate among the contributors to this volume. Allof us,
unlike the members of what has until recently been the main movement in
philosophy of science, do historical research and rely both on it and on
observation of contemporary scientists in developing our viewpoints. In
those viewpoints, furthermore, the descriptive and the normative are
inextricably mixed. Though we may differ in our standards and surely
differ about some matters of substance, we are scarcely to be distinguished
by our methods. The title of my earlier paper, ‘Logic of Discovery or
Psychology of Research?’ was not chosen to suggest what Sir Karl ought to
do but rather to describe what he does. When Lakatos writes, ‘But Kuhn’s
conceptual framework ... is socio-psychological: mine is normative’,! I
can only think that he is employing a sleight of hand to reserve the philo-
sophical mantle for himself. Surely Feyerabend is right in claiming that my
work repeatedly makes normative claims. Equally surely, though the point
will require more discussion, Lakatos’s position is social-psychological in
its repeated reliance on decisions governed not by logical rules but by the
mature sensibility of the trained scientist. If I differ from Lakatos (or
Sir Karl, Feyerabend, Toulmin, or Watkins), it is with respect to sub-
stance rather than method.

As to substance, our most apparent difference is about normal science,
the topic to which I shall turn immediately after discussing method. A
disproportionate part of this volume is devoted to normal science, and it
calls forth some of the oddest rhetoric: normal science does not exist and
is uninteresting. On this issue we do disagree, but not, I think, either
consequentially or in the ways my critics suppose. When I take it up, I shall
deal in part with the real difficulties in retrieving normal scientific traditions
from history, but my first and more central point will be a logical one. The
existence of normal science is a corollary of the existence of revolutions, a
point implicit in Sir Karl’s paper and explicit in Lakatos’s. If it did not
exist (or if it were non-essential, dispensable for science), then revolutions
would be in jeopardy also. But, about the latter, I and my critics (excepting
Toulmin) agree. Revolutions through criticism demand normal science

no less than revolutions through crisis. Inevitably, the term ‘cross-purposes’
better catches the nature of our discourse than ‘disagreement.’
1 This volume, p. 177.

234 THOMAS 8. KUHN

Discussion of normal science raises the third set of issues about which
criticism has here clustered: the nature of the change from one normal-
scientific tradition to another and of the techniques by which the resulting
conflicts are resolved. My critics respond to my views on this subject with
charges of irrationality, relativism, and the defence of mob rule. These are
all labels which I categorically reject, even when they are used in my
defence by Feyerabend. To say that, in matters of theory-choice, the force
of logic and observation cannot in principle be compelling is neither to
discard logic and observation nor to suggest that there are not good reasons
for favouring one theory over another. To say that trained scientists are,
in such matters, the highest court of appeal is neither to defend mob rule
nor to suggest that scientists could have decided to accept any theory at all.
In this area, too, my critics and I differ, but our points of difference have
yet to be seen for what they are.

These three sets of issues—method, normal science, and mob rule—are
the ones which bulk largest in this volume and, for that reason, in my
response. But my reply cannot close without going one step beyond them
to consider the problem of paradigms to which Miss Masterman’s essay is
devoted. I concur in her judgement that the term ‘paradigm’ points to the
central philosophical aspect of my book but that its treatment there is
badly confused. No aspect of my viewpoint has evolved more since the book
was written, and her paper has helped in that development. Though my
present position differs from hers in many details, we approach the pro-
lem in the same spirit including a common conviction of the relevance of
the philosophy of language and of metaphor.

I shall not here be able to deal at all fully with the problems presented
by my initial treatment of paradigms, but two considerations necessitate
my touching upon them. Even brief discussion should permit the isolation
of two quite different ways in which the term is deployed in my book and
thus eliminate a constellation of confusions which has handicapped me as
well as my critics. The resulting clarification will, in addition, permit me to
suggest what I take to be the root of my single most fundamental difference
from Sir Karl.

He and his followers share with more traditional philosophers of science
the assumption that the problem of theory-choice can be resolved by tech-
niques which are semantically neutral. The observational consequences
of both theories are first stated in a shared basic vocabulary (not neces-
sarily complete or permanent). Some comparative measure of their truth/
falsity count then provides the basis for a choice between them. For Sir Karl
and his school, no less than for Carnap and Reichenbach, canons of rationa-
lity thus derive exclusively from those of logical and linguistic syntax. Paul

REFLECTIONS ON MY CRITICS 235

Feyerabend provides the exception which proves that rule. Denying the
existence of a vocabulary adequate to neutral observation reports, he at
once concludes to the intrinsic irrationality of theory-choice.

That conclusion is surely Pickwickian. No process essential to scientific
development can be labelled ‘irrational’ without vast violence to the term.
It is therefore fortunate that the conclusion is unnecessary. One can deny,
as Feyerabend and I do, the existence of an observation language shared
in its entirety by two theories and still hope to preserve good reasons for
choosing between them. To achieve that goal, however, philosophers of
science will need to follow other contemporary philosophers in examining,
to a previously unprecedented depth, the manner in which language fits
the world, asking how terms attach to nature, how those attachments
are learned, and how they are transmitted from one generation to an-
other by the members of a language community. Because paradigms, in
one of the two separable senses of the term, are fundamental to my own
attempts to answer questions of that sort, they must also find a place in
this essay.

2. METHODOLOGY: THE ROLE OF HISTORY AND SOCIOLOGY

Doubts about the appropriateness of my methods te my conclusions
unite many of the essays in this volume. History and social-psychology are
not, my critics claim, a proper basis for philosophical conclusions. Their
reservations are not, however, all of a piece. I shall therefore consider
seriatim the somewhat different forms they take in the essays by Sir Karl,
Watkins, Feyerabend, and Lakatos.

Sir Karl concludes his paper by pointing out that to him ‘the idea of
turning for enlightenment concerning the aims of science, and its possible
progress, to sociology or psychology (or... to the history of science) is
surprising and disappointing. . . . how,’ he asks, ‘can the regress to these
often spurious sciences help us in this particular difficulty?’ I am puzzled
to know what these remarks intend, for in this area I think there are no
differences between Sir Karl and myself. If he means that the generaliza-
tions which constitute received theories in sociology and psychology (and
history?) are weak reeds from which to weave a philosophy of science, I
could not agree more heartily. My work relies on them no more than his.
If, on the other hand, he is challenging the relevance to philosophy of
science of the sorts of observations collected by historians and sociologists,
I wonder how his own work is to be understood. His writings are crowded
with historical examples and with generalizations about scientific be-
haviour, some of them discussed in my earlier essay. He does write on

1 This volume, pp. 57-8.

236 THOMAS S. KUHN

historical themes, and he cites those papers in his central philosophical
works. A consistent interest in historical problems and a willingness to en-
gage in original historical research distinguishes the men he has trained
from the members of any other current school in philosophy of science.
On these points I am an unrepentant Popperian.

John Watkins voices a different sort of doubt. Early in his paper he
writes that ‘methodology . . . is concerned with science at its best, or with
science as it should be conducted, rather than with hack science,”! a point
with which, at least in a more careful formulation, I fully agree. Later he
argues that what I have called normal science is hack science, and he then
asks why I am so ‘concerned to up-value Normal Science and down-value
Extraordinary Science?” In so far as that question is about normal science
in particular, I reserve my response until later (at which point I shall
attempt also to unravel Watkins’s extraordinary distortion of my position).
But Watkins seems also to be asking a more general question, one that
relates closely to an issue raised by Feyerabend. Both grant, at least for the
sake of their argument, that scientists do behave as I have said they do (I
shall later consider their qualifications of that concession). Why should the
philosopher or methodologist, they then ask, take the facts seriously? He is,
after all, concerned not with a full description of science but with the dis-
covery of the essentials of the enterprise, i.e., with rational reconstruction.
By what right and what criteria does the historian-observer or sociologist-
observer tell the philosopher which facts of scientific life he must include
in his reconstruction, which he may ignore?

To avoid lengthy disquisitions on the philosophy of history and of
sociology, I restrict myself to a personal response. I am no less concerned
with rational reconstruction, with the discovery of essentials, than are
philosophers of science. My objective, too, is an understanding of science,
of the reasons for its special efficacy, of the cognitive status of its theories.
But unlike most philosophers of science, I began as an historian of science,
examining closely the facts of scientific life. Having discovered in the
process that much scientific behaviour, including that of the very greatest
scientists, persistently violated accepted methodological canons, I had to
ask why those failures to conform did not seem at all to inhibit the success
of the enterprise. When I later discovered that an altered view of the nature
of science transformed what had previously seemed aberrant behaviour into
an essential part of an explanation for science’s success, the discovery was
a source of confidence in that new explanation. My criterion for empha-
sizing any particular aspect of scientific behaviour is therefore not simply
that it occurs, nor merely that it occurs frequently, but rather that it fits a

1 This volume, p. 27. 2? This volume, p. 31.

REFLECTIONS ON MY CRITICS 237

theory of scientific knowledge. Conversely, my confidence in that theory
derives from its ability to make coherent sense of many facts which, on an
older view, had been either aberrant or irrelevant. Readers will observe a
circularity in the argument, but it is not vicious, and its presence does not
at all distinguish my view from those of my present critics, Here, too, I am
behaving as they do.

That my criteria for discriminating between the essential and non-
essential elements of observed scientific behaviour are to a significant
extent theoretical provides also an answer to what Feyerabend calls the
ambiguity of my presentation. Are Kuhn’s remarks about scientific develop-
ment, he asks, to be read as descriptions or prescriptions?! The answer, of
course, is that they should be read in both ways at once. If I have a theory
of how and why science works, it must necessarily have implications for the
way in which scientists should behave if their enterprise is to flourish. The
structure of my argument is simple and, I think, unexceptionable: scientists
behave in the following ways; those modes of behaviour have (here theory
enters) the following essential functions; in the absence of an alternate
mode that would serve similiar functions, scientists should behave essen-
tially as they do if their concern is to improve scientific knowledge.

Note that nothing in that argument sets the value of science itseJf, and
that Feyerabend’s ‘plea for hedonism’ is correspondingly irrelevant.?
Partly because they have misconstrued my prescription (a point to which
I shall return), both Sir Karl and Feyerabend find menace in the enter-
prise I have described. It is ‘liable to corrupt our understanding and dim-
inish our pleasure’ (Feyerabend); it is ‘a danger . . . indeed to our civiliza-
tion’ (Sir Karl).3 I am not led to that evaluation nor are many of my readers,
but nothing in my argument depends on its being wrong. To explain why
an enterprise works is not to approve or disapprove it.

Lakatos’s paper raises a fourth problem about method, and it is the most
fundamental of all. I have already confessed my inability to understand
what he means when he says things like, ‘Kuhn’s conceptual framework ...
is socio-psychological: mine is normative’. If I ask, however, not what he
intends, but why he finds this sort of rhetoric appropriate, an important
point emerges, one that is almost explicit in the first paragraph of his
section 4. Some of the principles deployed in my explanation of science
are irreducibly sociological, at least at this time. In particular, confronted
with the problem of theory-choice, the structure of my response runs
roughly as follows: take a group of the ablest available people with the

1 This volume, p. 198. For a far deeper and more careful examination of some contexts
in which the descriptive and normative merge, see Cavell [1969].

2 This volume, p. 209.

3 This volume, pp. 209 and 53.

238 THOMAS S. KUHN

most appropriate motivation; train them in some science and in the
specialties relevant to the choice at hand ; imbue them with the value system,
the ideology, current in their discipline (and to a great extent in other
scientific fields as well); and, finally, let them make the choice. If that tech-
nique does not account for scientific development as we know it, then no
other will. There can be no set of rules of choice adequate to dictate
desired individual behaviour in the concrete cases that scientists will meet
in the course of their careers. Whatever scientific progress may be, we
must account for it by examining the nature of the scientific group, dis-
covering what it values, what it tolerates, and what it disdains.

That position is intrinsically sociological and, as such, a major retreat
from the canons of explanation licensed by the traditions which Lakatos
labels justificationism and falsificationism, both dogmatic and naive. I shall
later specify it further and defend it. But my present concern is simply
with its structure, which both Lakatos and Sir Karl find unacceptable in
principle. My question is, why should they? Both repeatedly use argu-
ments of the same structure themselves.

Sir Karl does not, it is true, do so all the time. That part of his writing
which seeks an algorithm for verisimilitude would, if successful, eliminate
all need for recourse to group values, to judgements made by minds pre-
pared in a particular way. But, as I pointed out at the end of my previous
essay, there are many passages throughout Sir Karl’s writings which can
only be read as descriptions of the values and attitudes which scientists
must possess if, when the chips are down, they are to succeed in advancing
their enterprise. Lakatos’s sophisticated falsificationism goes even further.
In all but a few respects, only two of them essential, his position is now
very close to my own. Among the respects in which we agree, though he
has not yet seen it, is our common use of explanatory principles that are
ultimately sociological or ideological in structure.

Lakatos’s sophisticated falsificationism isolates a number of issues about
which scientists employing the method must make decisions, individually
or collectively. (I distrust the term ‘decision’ in this context since it implies
conscious deliberation on each issue prior to the assumption of a research
stance. For the moment, however, I shall use it. Until the last section of
this paper very little will depend upon the distinction between making a
decision and finding oneself in the position that would have resulted from
making it.) Scientists must, for example, decide which statements to make
‘unfalsifiable by fiat’ and which not. Or, dealing with a probabilistic theory,
they must decide on a probability threshold below which statistical evidence
will be held ‘ “inconsistent” ’ with that theory.? Above all, viewing theories

1 This volume, p. 106. 3 This volume, p. 109.

REFLECTIONS ON MY CRITICS 239

as research programmes to be evaluated over time, scientists must decide
whether a given programme at a given time is ‘progressive’ (whence scien-
tific) or ‘degenerative’ (whence pseudo-scientific).! If the first, it is to be
pursued; if the latter, rejected.

Notice now that a call for decisions like these may be read in two ways.
It may be taken to name or describe decision points for which procedures
applicable in concrete cases must still be supplied. On this reading Lakatos
has yet to tell us how scientists are to select the particular statements that
are to be unfalsifiable by their fiat; he must also still specify criteria which
can be used at the time to distinguish a degenerative from a progressive
research programme; and so on. Otherwise, he has told us nothing at all.
Alternatively, his remarks about the need for particular decisions may be read
as already complete descriptions (at least in form—their particular content
may be preliminary) of directives, or maxims which the scientist is required
to follow. On this interpretation, the third decision directive would read:
‘As a scientist, you may not refrain from deciding whether your research
programme is progressive or degenerative, and you must take the con-
sequences of your decision, abandoning the programme in one case, pur-
suing it in the other.’ Correspondingly, the second directive would read:
‘Working with a probabilistic theory, you must constantly ask yourself
whether the result of some particular experiment is not so improbable as
to be inconsistent with your theory, and you must, as a scientist, also
answer.’ Finally, the first directive would read: ‘As a scientist, you will
have to take risks, choosing certain statements as the basis for your work
and ignoring, at least until your research programme has developed, all
actual and potential attacks upon them.’

The second reading is, of course, far weaker than the first. It demands the
same decisions, but it neither supplies nor promises to supply rules which
would dictate their outcomes. Instead, it assimilates these decisions to
judgements of value (a subject about which I shall have more to say)
rather than to measurements or computations, say, of weight. Neverthe-
less, conceived merely as imperatives which commit the scientist to
making certain sorts of decisions, these directives are strong enough to
affect scientific development profoundly. A group whose members felt
no obligations to wrestle with such decisions (but which instead em-
phasized others, or none at all) would behave in notably different ways,
and their discipline would change accordingly. Though Lakatos’s dis-
cussion of his decision-directives is often equivocal, I believe that it is just
this second sort of efficacy upon which his methodology depends. Cer-
tainly he does little to specify algorithms by which the decisions he

1 This volume, pp. 118 ff,

240 THOMAS S. KUHN

demands are to be made, and the tenor of his discussion of naive and dog-
matic falsificationism suggests that he no longer thinks such specification
possible. In that case, however, his decision-imperatives are, in form
though not always in content, identical to my own. They specify ideolo-
gical commitments which scientists must share if their enterprise is to
succeed. They are therefore irreducibly sociological in the same sense and
to the same extent as my explanatory principles.

Under these circumstances I am not sure what Lakatos is criticizing or
what, in this area, he thinks we disagree about. A strange footnote late in
his paper may, however, provide a clue?:

“There are two kinds of psychologistic philosophies of science. According to one kind
there can be no philosophy of science: only a psychology of individual scientists.
According to the other kind there is a psychology of the “scientific,” “ideal,” or

“normal” mind: this turns philosophy of science into a psychology of this ideal
mind. ... Kuhn does not seem to have noticed this distinction.’

If I understand him correctly, Lakatos identifies the first kind of psycho-
logistic philosophy of science with me, the second with himself. But he is
misunderstanding me. We are not nearly so far apart as his description
would suggest, and, where we do differ, his literal position would demand
a renunciation of our common goal.

Part of what Lakatos is rejecting is explanations that demand recourse
to the factors which individuate particular scientists (‘the psychology
of the individual scientist’ versus ‘the psychology of the... “normal”
mind’). But that does not separate us. My recourse has been exclusively
to social psychology (I prefer ‘sociology’), a field quite different from indi-
vidual psychology reiterated m times. Correspondingly, my unit for pur-
poses of explanation is the normal (i.e. non-pathological) scientific group,
account being taken of the fact that its members differ but not of what
makes any given individual unique. In addition, Lakatos would like to
reject those characteristics of even normal scientific minds which make
them the minds of human beings. Apparently he sees no other way to
retain the methodology of an ideal science in explaining the observed
success of actual science. But his way will not do if he hopes to explain
an enterprise practiced by people. There are no ideal minds, and the
‘psychology of this ideal mind’ is therefore unavailable as a basis for explan-
ation. Nor is Lakatos’s manner of introducing the ideal needed to achieve
what he aims at. Shared ideals affect behaviour without making those who
hold them ideal. The type of question I ask has therefore been: how will a
particular constellation of beliefs, values, and imperatives affect group
behaviour? My explanations follow from the answer, I am not sure Lakatos

1 This volume, p. 180, footnote 3.

REFLECTIONS ON MY CRITICS 241

means anything else, but, if he does not, there is nothing in this area for us
to disagree about.

Having misconstrued the sociological base of my position, Lakatos and
my other critics inevitably fail to note a special feature which follows from
taking the normal group rather than the normal mind as unit. Given a
shared algorithm adequate, let us say, to individual choice between com-
peting theories or to the identification of severe anomaly, all members of a
scientific group will reach the same decision, That would be the case even
if the algorithm were probabilistic, for all those who used it would evaluate
the evidence in the same way. The effects of a shared ideology, however,
are less uniform, for its mode of application is of a different sort. Given a
group all the members of which are committed to choosing between
alternative theories and also to considering such values as accuracy, sim-
plicity, scope, and so on while making their choice, the concrete decisions
of individual members in individual cases will nevertheless vary. Group
behaviour will be affected decisively by the shared commitments, but
individual choice will be a function also of personality, education, and the
prior pattern of professional research. (These variables are the province of
individual psychology.) To many of my critics this variability seems a
weakness of my position. When considering the problems of crisis and of
theory-choice I shall want, however, to argue that it is instead a strength.
If a decision must be made under circumstances in which even the most
deliberate and considered judgement may be wrong, it may be vitally
important that different individuals decide in different ways. How else
could the group as a whole hedge its bets?

3. NORMAL SCIENCE: ITS NATURE AND FUNCTIONS

As to methods, then, the ones I employ are not significantly different from
those of my Popperian critics. Applying those methods, we, of course, draw
somewhat different conclusions, but even they are not so far apart as
several of my critics believe. In particular, all of us excepting Toulmin
share the conviction that the central episodes in scientific advance—those
which make the game worth playing and the play worth studying—are
revolutions, Watkins is constructing an opponent from his own straw
when he describes me as having ‘down-valued’ scientific revolutions, taken
a ‘philosophical dislike’ to them, or suggested that they ‘can hardly be
called science at all.’* Discovering the puzzling nature of revolutions was

1 If human motivation were not at issue, the same effect could be achieved by first
computing a probability and then assigning a certain fraction of the profession to each of
the competing theories, the exact fraction to depend on the result of the probabilistic
computation. Somehow that alternative makes my point by reductio ad absurdum.

2 This volume, pp. 31, 32 and 29.

242 THOMAS S. KUHN

what drew me to history and philosophy of science in the first place.
Almost everything I have written since deals with them, a fact which
Watkins points out and then ignores.

If, however, we agree about this much, we cannot altogether disagree
about normal science, the aspect of my work which most disturbs my
present critics. By their nature revolutions cannot be the whole of science:
something different must necessarily go on in between. Sir Karl sets up the
point admirably. Underlining what I have always recognized as one of our
principle areas of agreement, he stresses that ‘scientists necessarily de-
velop their ideas within a definite theoretical framework’.’ For him, as
for me, furthermore, revolutions demand such frameworks, since they
always involve the rejection and replacement of a framework or of some
of its integral parts. Since the science which I call normal is precisely
research within a framework, it can only be the opposite side of a coin the
face of which is revolutions. No wonder Sir Karl has been ‘dimly aware of
the distinction’ between normal science and revolutions.” It follows from
his premises.

Something else follows as well. If frameworks are necessary to scientists,
if to break with one is inevitably to break into another—points which Sir
Karl embraces explicitly—then the hold of a framework on a scientist’s
mind may not be accounted for merely as the result of his having ‘been
badly taught, . . . a victim of indoctrination’. Nor may it, as Watkins sup-
poses, be explained entirely by reference to the prevalence of third-rate
minds, fit only for ‘plodding, uncritical’ work.* Those things do exist, and
most of them do damage. Nevertheless, if frameworks are the prerequisite
of research, their grip on the mind is not merely ‘Pickwickian’, nor can it
be quite right to say that, ‘if we try, we can break out of our framework at
any time’.> To be simultaneously essential and freely dispensible is very
nearly a contradiction in terms. My critics become incoherent when they
embrace it.

None of that is said in an effort to show that my critics really agree with
me, if only they knew it. They do not! Rather I am trying, by eliminating
irrelevancies, to discover what we disagree about. I have so far argued that
Sir Karl’s phrase ‘revolutions in permanence’ does not, any more than
‘square-circle’, describe a phenomenon that could exist. Frameworks must
be lived with and explored before they can be broken. But that does not
imply that scientists ought not aim at perpetual framework-breaking, how-
ever unobtainable that goal. ‘Revolutions in permanence’ could name an

1 This volume, p. 51, italics added. Unless explicitly noted all italic passages in the
quotations in this paper are in the originals. 2 This volume, p. 52.
3 This volume, p. 53. 4 This volume, p. 32. § This volume, p. 56

REFLECTIONS ON MY CRITICS 243

important ideological imperative. If Sir Karl and I disagree at all about
normal science, it is over this point. He and his group argue that the
scientist should try at all times to be a critic and a proliferator of alternate
theories. I urge the desirability of an alternate strategy which reserves
such behaviour for special occasions.

That disagreement, being restricted to research strategy, is already
narrower than the one my critics have envisaged. To see what is at stake
it must be narrowed further. Everything that has been said so far, though
phrased for science and scientists, applies equally to a number of other
fields. My methodological prescription is, however, directed exclusively to
the sciences and, among them, to those fields which display the special
developmental pattern known as progress. Sir Karl neatly catches the
distinction I have in mind. At the start of his paper he writes: ‘ ‘‘A scientist
engaged in a piece of research . . . can go at once to the heart of .. . an
organized structure. . . [and of] a generally accepted problem-situation . ..
[leaving] it to others to fit his contribution into the framework of scientific
knowledge.” ... the philosopher’, he continues, ‘finds himself in a
different position.’! Nevertheless, having pointed to the difference, Sir
Karl thereafter ignores it, recommending the same strategy to both
scientists and philosophers. In the process he misses the consequences for
research design of the special detail and precision with which, as he says,
the framework of a mature science informs its practitioners what to do. In
the absence of that detailed guidance, Sir Karl’s critical strategy seems to me
the very best available. It will not induce the special developmental
pattern which characterizes, say, physics, but neither will any other
methodological prescription. Given a framework which does provide such
guidance, however, then I do intend my methodological recommendations
to apply.

Consider for a moment the evolution of philosophy or of the arts since
the end of the Renaissance. These are fields often contrasted with the
established sciences as ones which do not progress. That contrast cannot
be due to the absence of revolutions or of an intervening mode of normal
practice. On the contrary, long before the similar structure of scientific
development was noticed, historians portrayed these fields as developing
through a succession of traditions punctuated by revolutionary alterations
of artistic style and taste or of philosophical viewpoint and goal. Nor can
the contrast be due to the absence from philosophy and the arts of a
Popperian methodology. As Miss Masterman observes for philosophy,?

1 This volume, p. 51. Readers who know my [1962a] will recognize how closely Sir
Karl’s phrase ‘leaving it to others to fit his contribution into the framework of scientific
knowledge’ catches the essential implications of my description of normal science.

2 This volume, pp. 69 ff.

244 THOMAS 8. KUHN

these are just the fields in which it is best exemplified, in which prac-
titioners do find current tradition stifling, do struggle to break with it, and
do regularly seek a style or a philosophical viewpoint of their own. In the
arts, in particular, the work of men who do not succeed in innovation is
described as ‘derivative’, a term of derogation significantly absent from
scientific discourse which does, on the other hand, repeatedly refer to
‘fads’. In none of these fields, whether arts or philosophy, does the prac-
titioner who fails to alter traditional practice have significant impact on
the discipline’s development.! These are, in short, fields to which Sir
Karl’s method is essential because without constant criticism and the pro-
liferation of new modes of practice there would be no revolutions. Sub-
stituting my own methodology for Sir Karl’s would induce stagnation for
exactly the reasons my critics underscore. In no obvious sense, however,
does his methodology produce progress. The relation of pre- to post-
revolutionary practice in these fields is not what we have learned to expect
from the developed sciences.

My critics will suggest that the reasons for that difference are obvious.
Fields like philosophy and the arts do not claim to be sciences, nor do they
satisfy Sir Karl’s demarcation criterion. They do not, that is, generate
results which can in principle be tested through a point-by-point com-
parison with nature. But that argument seems to me mistaken. Without
satisfying Sir Karl’s criterion these fields could not be sciences, but they
could nevertheless progress as the sciences do. In antiquity and during
the Renaissance, the arts rather than the sciences provided the accepted
paradigms of progress.? Few philosophers find reasons of principle why
their field should not move steadily ahead, though many bemoan its failure
to do so. In any case, there are many fields—I shall call them proto-
sciences—in which practice does generate testable conclusions but which
nonetheless resemble philosophy and the arts rather than the established
sciences in their developmental patterns. I think, for example, of fields
like chemistry and electricity before the mid-eighteenth century, of the
study of heredity and phylogeny before the mid-nineteenth, or of many of
the social sciences today. In these fields, too, though they satisfy Sir Karl’s
demarcation criterion, incessant criticism and continual striving for a fresh
start are primary forces, and need to be. No more than in philosophy and
the arts, however, do they result in clear-cut progress.

I conclude, in short, that the proto-sciences, like the arts and phil-
osophy, lack some element which, in the mature sciences, permits the

1 For a fuller discussion of differences between scientific and artistic communities and
between the corresponding developmental patterns, see my [1969].
2 Gombrich [1960], pp. 13 ff.

REFLECTIONS ON MY CRITICS 245

more obvious forms of progress. It is not, however, anything that a method-
ological prescription can provide. Unlike my present critics, Lakatos at
this point included, I claim no therapy to assist the transformation of a
proto-science to a science, nor do I suppose that anything of the sort is to
be had. If, as Feyerabend suggests, some social scientists take from me the
view that they can improve the status of their field by first legislating
agreement on fundamentals and then turning to puzzle solving, they are
badly misconstruing my point.? A sentence I once used when discussing
the special efficacy of mathematical theories applies equally here: ‘As in
individual development, so in the scientific group, maturity comes most
surely to those who know how to wait.” Fortunately, though no pre-
scription will force it, the transition to maturity does come to many fields,
and it is well worth waiting and struggling to attain. Each of the currently
established sciences has emerged from a previously more speculative
branch of natural philosophy, medicine, or the crafts at some relatively
well-defined period in the past. Other fields will surely experience the
same transition in the future. Only after it occurs does progress become an
obvious characteristic of a field. And only then do those prescriptions of
mine which my critics decry come into play.

About the nature of that change I have written at length in my Scientific
Revolutions and more briefly when discussing demarcation criteria in my
earlier contribution to this volume. Here I shall be content with an abstract
descriptive summary. Confine attention first to fields which aim to explain
in detail some range of natural phenomena. (If, as my critics point out,
my further description fits theology and bank-robbery as well, no prob-
lems are thereby created.) Such a field first gains maturity when provided
with theory and technique which satisfy the four following conditions.
First is Sir Karl’s demarcation criterion without which no field is poten-
tially a science: for some range of natural phenomena concrete predictions
must emerge from the practice of the field. Second, for some interesting
sub-class of phenomena, whatever passes for predictive success must be
consistently achieved. (Ptolemaic astronomy always predicted planetary
position within widely recognized limits of error. The companion astro-
logical tradition could not, excepting for the tides and the average men-
strual cycle, specify in advance which prediction would succeed, which
fail.) Third, predictive techniques must have roots in a theory which, how-
ever metaphysical, simultaneously justifies them, explains their limited
success, and suggests means for their improvement in both precision and

1 This volume, p. 198. Note, however, that the passage Feyerabend quotes in footnote 3
does not say at all what he reports.
2 See p. 190 of my [19628].

246 THOMAS 8S. KUHN

scope. Finally, the improvement of predictive technique must be a chal-
lenging task, demanding on occasions the very highest measure of talent
and devotion.

These conditions are, of course, tantamount to the description of a good
scientific theory. But once hope for a therapeutic prescription is aban-
doned, there is no reason to expect anything less. My claim has been—it is
my single genuine disagreement with Sir Karl about normal science—that
with such a theory in hand the time for steady criticism and theory pro-
liferation has passed. Scientists for the first time have an alternative which
is not merely aping what has gone before. They can instead apply their
talents to the puzzles which lie in what Lakatos now calls the ‘protective
belt’. One of their objectives then is to extend the range and precision of
existing experiment and theory as well as to improve the match between
them. Another is to eliminate conflicts both between the different theories
employed in their work and between the ways in which a single theory is
used in different applications. (Watkins is right, I now think, in charging
that my book gives too small a role to these inter-and intra-theoretic
puzzles, but Lakatos’s attempt to reduce science to mathematics, leaving
no significant role to experiment, goes vastly too far. He could not, for
example, be more mistaken about the irrelevance of the Balmer formula to
the development of Bohr’s atom model.1) These puzzles and others like
them constitute the main activity of normal science. Though I cannot
argue the point again, they are not, pace Watkins, for hacks, nor do they,
pace Sir Karl, resemble the problems of applied science and engineering.
Of course the men fascinated by them are a special breed, but so are phil-
osophers or artists.

Even given a theory which permits normal science, however, scientists
need not engage the puzzles it supplies. They could instead behave as
practitioners of the proto-sciences must; they could, that is, seek potential
weak spots, of which there are always large numbers, and endeavour to
erect alternate theories around them. Most of my present critics believe
they should do so. I disagree but exclusively on strategic grounds. Feyera-
bend mispresents me in a way I particularly regret when he reports, for
example, that I ‘criticized Bohm for disturbing the uniformity of the con-
temporary quantum theory’.? My record as a trouble maker should be hard
to reconcile with that report. In fact, I confessed to Feyerabend that I
shared Bohm’s discontent but thought his exclusive attention to it almost

1 This volume, p. 147, for the remarks on the Balmer formula. This attitude towards
the role of experiment is found throughout much of Lakatos’s paper. For the actual role of
the Balmer formula in Bohr’s work, see the paper cited in footnote 3, p. 256 below.

2 This volume, p. 206. An implicit answer to the contrast Feyerabend draws between my
attitudes towards Bohm and Einstein as critics will be found below, on pp. 257ff.

REFLECTIONS ON MY CRITICS 247

certain to fail. No one, I suggested, was likely to resolve the paradoxes of
the quantum theory until he could relate them to some concrete technical
puzzle of current physics. In the developed sciences, unlike philosophy, it
is technical puzzles that provide the usual occasion and often the concrete
materials for revolution. Their availability together with the information
and signals they provide account in large part for the special nature of
scientific progress. Because they can ordinarily take current theory for
granted, exploiting rather than criticizing it, the practitioners of mature
sciences are freed to explore nature to an esoteric depth and detail other-
wise unimaginable. Because that exploration will ultimately isolate severe
trouble spots, they can be confident that the pursuit of normal science will
inform them when and where they can most usefully become Popperian
critics. Even in the developed sciences, there is an essential role for Sir
Karl’s methodology. It is the strategy appropriate to those occasions when
something goes wrong with normal science, when the discipline encounters
crisis.

I have discussed those points at great length elsewhere and shall not
elaborate them here. Let me instead conclude this section by returning to
the generalization with which it began. Despite the energy and space which
my critics have devoted to it, I do not think the position just outlined
departs very greatly from Sir Karl’s. On this set of questions our differ-
ences are over nuances. I hold that in the developed sciences occasions for
criticism need not, and by most practitioners ought not, deliberately be
sought. When they are found, a decent restraint is the appropriate first
response. Sir Karl, though he sees the need to defend a theory when first
attacked, gives more emphasis than I to the purposeful search for weak
points. There is not a great deal to choose between us.

Why is it, then, that my present critics see our crucial differences here?
One reason I have already suggested: their sense—which I do not share
but which is in any case irrelevant—that my strategic prescription violates
a higher morality. A second reason, which I shall discuss in the next section,
is their apparent inability to see in historical examples the detailed func-
tions of the breakdown of normal science in setting the stage for revolu-
tions. Lakatos’s case histories are in this respect particularly interesting,
for he describes clearly the transition from the progressive to the de-
generative phase of a research programme (the transition from normal
science to crisis) and then appears to deny the critical importance of what
results. With a third reason, however, I must deal at this point. It emerges
from a criticism voiced by Watkins, which, however, in the present con-
text serves a purpose he by no means intends.

‘By contrast with the relatively sharp idea of testability,’ Watkins

248 THOMAS S. KUHN

writes, ‘the notion of [normal science’s] ‘‘ceasing adequately to support a
puzzle-solving tradition” is essentially vague.’! With the charge of vague~
ness I agree, but it is a mistake to suppose that it differentiates my position
from Sir Karl’s. What is precise about Sir Karl’s position is, as Watkins
also points out, the idea of testability in principle. On that much I rely
too, for no theory that was not in principle testable could function or cease
to function adequately when applied to scientific puzzle solving. I do,
despite Watkins’s strange failure to see it, take Sir Karl’s notion of the
asymmetry of falsification and confirmation very seriously indeed. What is
vague, however, about my position is the actual criteria (if that is what is
called for) to be applied when deciding whether a particular failure in
puzzle-solving is or is not to be attributed to fundamental theory and thus
to become an occasion for deep concern. That decision is, however, identi-
cal in kind with the decision whether or not the result of a particular test
actually falsifies a particular theory, and on that subject Sir Karl is nec-
essarily as vague as I. To drive a wedge between us on this issue, Watkins
transfers the sharpness of testability-in-principle to the shady area of
testability-in-practice without even hinting how the transfer is to be
effected. It is not an unprecedented mistake, and it regularly makes Sir
Karl’s methodology appear more a logic, less an ideology, than it is.
Besides, reverting to a point made at the end of the last section, one may
legitimately ask whether what Watkins calls vagueness is a disadvantage.
All scientists must be taught—it is a vital element in their ideology—to be
alert for and responsible to theory-breakdown, whether it be described as
severe anomaly or falsification. In addition, they must be supplied with
examples of what their theories can, with sufficient care and skill, be ex-
pected to do. Given only that much, they will, of course, often reach
different judgements in concrete cases, one man seeing a cause of crisis
where another sees only evidence of limited talent for research. But they
do reach judgements, and their lack of unanimity may then be what saves
their profession. Most judgements that a theory has ceased adequately to
support a puzzle-solving tradition prove to be wrong. If everyone agreed
in such judgements, no one would be left to show how existing theory could
account for the apparent anomaly as it usually does. If, on the other hand,
no one were willing to take the risk and then seek an alternate theory, there
would be none of the revolutionary transformations on which scientific
development depends. As Watkins says, ‘there must be a critical level at
which a tolerable turns into an intolerable amount of anomaly’.? But that
level ought not be the same for everyone, nor need any individual specify
his own tolerance level in advance. He need only be certain that he has one

1 This volume, p. 30. 2 This volume, p. 30.

REFLECTIONS ON MY CRITICS 249

and aware of some sorts of discrepancies which would drive him towards
it.

4. NORMAL SCIENCE: ITS RETRIEVAL FROM HISTORY

I have so far argued that, if there are revolutions, then there must be
normal science. One may, however, legitimately ask whether either exists.
Toulmin has done so, and my Popperian critics have difficulties in re-
trieving from history a significant normal science upon the existence of
which that of revolutions depends. Toulmin’s questions are of particular
value, for a response to them will require me to confront some genuine
difficulties presented by my Scientific Revolutions and to modify my
original presentation accordingly. Unfortunately, however, those diffi-
culties are not the ones Toulmin sees. Before they can be isolated, the dust
he has imported must be swept away.

Though there have been important changes in my position during the
seven years since my book was published, the retreat from a concern with
macro- to a concentration on micro-revolutions is not among them. Part of
that retreat Toulmin finds by contrasting a paper read in 1961 with a book
published in 1962.1 The paper was, however, both written and published after
the book, and its first footnote specifies the relationship which Toulmin
inverts. Other evidence of retreat Toulmin retrieves from a comparison of
the book with the manuscript of my first essay in this volume.? But no one
zlse has, to my knowledge, even noticed the differences which he under-
ines, and the book is in any case quite explicit about the centrality of the
concern which Toulmin finds only in my more recent work. Among the
revolutions discussed in the body of the book are, for example, discoveries
like those of X-rays and of the planet Uranus. ‘Admittedly’, the preface
states, ‘the extension [of the term “revolution” to episodes like these]
strains customary usage. Nevertheless, I shall continue to speak even of
liscoveries as revolutionary, because it is just the possibility of relating
‘heir structure to that of, say, the Copernican revolution that makes the
xtended conception seem to me so important.’ My concern, in short, has
ever been with scientific revolutions as ‘something that tended to happen
na given branch of science only once every two hundred years or so’.4
Rather it has been throughout what 'Toulmin now takes it to have become:
\ little studied type of conceptual change which occurs frequently in

1 This volume, p. 39 ff.

* See also Toulmin [1967], especially p. 471, footnote 8. The publication of this bio-
sraphical canard in advance of the article on which it claims to be based has given me much
rouble.

3 Cf. my [1962a], pp. 7 f. On p. 6 the possibility of extending the conception to micro-
evolutions is described as ‘a fundamental thesis’ of the book. ‘ This volume, p. 44.

250 THOMAS Ss. KUHN

science and is fundamental to its advance.

To that concern Toulmin’s geological analogy is entirely appropriate,
but not in the way he uses it. He emphasizes the aspect of the uniformi-
tarian-catastrophist debate which dealt with the possibility of attributing
catastrophes to natural causes, and he suggests that once that issue had
been resolved ‘ “catastrophes” became uniform and law-governed just like
any other geological and palaeontological phenomena’.! But his insertion
of the term ‘uniform’ is gratuitous. Besides the issue of natural causes, the
debate had a second central aspect: the question whether catastrophes
existed, whether a major role in geological evolution should be attributed
to phenomena like earthquakes and volcanic action which acted more sud-
denly and destructively than erosion and sedimentary deposition. This
part of the debate the uniformitarians lost. When it was over, geologists
recognized two sorts of geological change, no less distinct because both due
to natural causes; one acted gradually and uniformly, the other suddenly
and catastrophically. Even today we do not treat tidal waves as special
cases of erosion.

Correspondingly, my claim has been, not that revolutions were inscrut-
able unit events, but that in science as in geology there are two sorts of
change. One of them, normal science, is the generally cumulative process
by which the accepted beliefs of a scientific community are fleshed out,
articulated, and extended. It is what scientists are trained to do, and the
main tradition in English-speaking philosophy of science derives from the
examination of the exemplary works in which that training is embodied.
Unfortunately, as indicated in my previous essay, proponents of that
philosophical tradition generally choose their examples from changes of
another sort which are then tailored to fit. The result is a failure to recog-
nize the prevalence of changes in which conceptual commitments funda-
mental to the practice of some scientific specialty must be jettisoned and
replaced. Of course, as Toulmin says, the two sorts of change interpene-
trate: revolutions are no more total in science than in other aspects of life,
but recognizing continuity through revolutions has not led historians or
anyone else to abandon the notion. It was a weakness of my Scientific
Revolutions that it could only name, not analyse, the phenomenon it
repeatedly referred to as ‘partial communication’. But partial communica-
tion was never, as Toulmin would have it, ‘complete [mutual] incompre-

hension’.? It named a problem to be worked on, not elevated to inscruta-
bility. Unless we can learn more about it (I shall offer some hints in the
next section), we shall continue to mistake the nature of scientific progress
and thus perhaps of knowledge. Nothing in Toulmin’s essay begins to

1 This volume, p. 43; my italics.
® This volume, p. 43

REFLECTIONS ON MY CRITICS 251

persuade me that we shall succeed if we continue to treat all scientific
change as one.

The fundamental challenge of his paper, however, remains. Can we dis-
tinguish mere articulations and extensions of shared belief from changes
which involve reconstruction? The answer in extreme cases is obviously
‘Yes’. Bohr’s theory of the hydrogen spectrum was revolutionary as
Sommerfeld’s theory of the hydrogen fine-structure was not; Copernican
astronomical theory was revolutionary but the caloric theory of adiabatic
compression was not. These examples are, however, too extreme to be
fully informative: there are too many differences between the theories
contrasted, and the revolutionary changes affected too many people. For-
tunately, however, we are not restricted to them: Ampére’s theory of the
electric circuit was revolutionary (at least among French electricians),
because it severed electric-current and electrostatic effects which had
previously been conceptually united. Ohm’s Law was again revolutionary,
and was resisted accordingly, because it demanded a reintegration of con-
cepts previously applied separately to current and charge.! On the other
hand, the Joule-Lenz law relating the heat generated in a wire to the
resistance and current was a product of normal science, for both the
qualitative effects and the concepts required for quantification were in
hand. Again, at a level which is not so obviously theoretical, Lavoisier’s
discovery of oxygen (though perhaps not Scheele’s and surely not Priestley’s)
was revolutionary, for it was inseparable from a new theory of combustion
and acidity. The discovery of neon, however, was not, for helium had
supplied both the notion of an inert gas and the needed column of the
periodic table.

One may question, however, how far and how universally this process of
discrimination can be pressed. I am repeatedly asked whether such-and-
such a development was ‘normal or revolutionary’, and I usually have to
answer that I do not know. Nothing depends upon my, or anyone else’s,
being able to respond in every conceivable case, but much depends on the
discrimination’s being applicable to a far larger number of cases than have
been supplied so far. Part of the difficulty in answering is that the dis-
crimination of normal from revolutionary episodes demands close his-
torical study, and few parts of the history of science have received it. One
must know not simply the name of the change, but the nature and structure
of group commitments before and after it occurred. Often, to determine
these, one must also know the manner in which the change was received
when first proposed. (There is no area in which I am more deeply conscious
of the need for additional historical research, though I dissent from the

3 On these topics, see Brown [1969] and Schagrin [1963].

252 THOMAS 8. KUHN

conclusions Pearce Williams draws from that need and doubt that the results
of investigation will draw Sir Karl and me closer.) My difficulty, however,
has a deeper aspect. Though much depends upon more research, the in-
vestigations required are not simply of the sort indicated above, Further-
more, the structure of the argument in my Scientific Revolutions somewhat
obscures the nature of what is missing. If I were rewriting the book now I
would significantly change its organization.

The gist of the problem is that to answer the question ‘normal or
revolutionary?’ one must first ask, ‘for whom?’ Sometimes the answer is
easy: Copernican astronomy was a revolution for everyone; oxygen was a
revolution for chemists but not for, say, mathematical astronomers unless,
like Laplace, they were interested in chemical and thermal subjects too.
For the latter group oxygen was simply another gas, and its discovery was
merely an increment to their knowledge; nothing essential to them as
astronomers had to be changed in the discovery’s assimilation. It is not,
however, usually possible to identify groups which share cognitive commit-
ments simply by naming a scientifie subject matter—astronomy, chemistry,
mathematics, or the like. That is, however, what I have just done here and
did earlier in my book. Some scientific subjects, for example the study of
heat, have belonged to different scientific communities at different times,
sometimes to several at once without becoming the special province of any.
In addition, though scientists are much more nearly unanimous in their
commitments than practitioners of, say, philosophy and the arts, there are
such things as schools in science, communities which approach the same
subject from very different points of view. French electricians in the first
decades of the nineteenth century were members of a school which in-
cluded almost none of the British electricians of the day, and so on. If I
were writing my book again now, I would therefore begin by discussing
the community structure of science, and I would not rely exclusively on
shared subject matter in doing so. Community structure is a topic about
which we have very little information at present, but it has recently be-
come a major concern for sociologists, and historians are now increasingly
concerned with it as well.

The research problems involved are by no means trivial. Historians
of science who engage in them must cease to rely exclusively on the tech-
niques of the intellectual historian and use those of the social and cultural
historian as well. Even though work has scarcely begun, there is every
reason to expect it to succeed, particularly for the developed sciences,
those which have severed their historical roots in the philosophical or

1A somewhat more detailed discussion of this reorganization together with some pre-
liminary bibliography is included in my (1970].

REFLECTIONS ON MY CRITICS 253

medical communities. What one would then have would be a roster of the
different specialists’ groups through which science was advanced at various
periods of time. The analytic unit would be the practitioners of a given
specialty, men bound together by common elements in their education and
apprenticeship, aware of each other’s work, and characterized by the
relative fullness of their professional communication and the relative
unanimity of their professional judgement. In the mature sciences the
members of such communities would ordinarily see themselves and be
seen by others as the men exclusively responsible for a given subject
matter and a given set of goals, including the training of their successors.
Research would, however, disclose the existence of rival schools as well.
Typical communities, at least on the contemporary scientific scene, may
consist of a hundred members, sometimes significantly fewer. Individuals,
particularly the ablest, may belong to several such groups, either simul-
taneously or in succession, and they will change or at least adjust their
thinking caps as they go from one to another.

Groups like these should, I suggest, be regarded as the units which
produce scientific knowledge. They could not, of course, function without
individuals as members, but the very idea of scientific knowledge as a
private product presents the same intrinsic problems as the notion of a
private language, a parallel to which I shall return. Neither knowledge nor
language remains the same when conceived as something an individual can
possess and develop alone. It is, therefore, with respect to groups like these
that the question ‘normal or revolutionary?’ should be asked. Many
episodes will then be revolutionary for no communities, many others for
only a single small group, still others for several communities together, a
few for all of science. Posed in that way, the question will, I believe, have
answers as precise as my distinction requires. One reason for thinking so
I shall illustrate in a moment by applying this approach to some of the
concrete cases used by my critics to raise doubts about the existence and
role of normal science. First, however, I must point out one aspect of my
present position which, far more clearly than normal science, represents a
deep divide between my viewpoint and Sir Karl’s.

The programme just outlined makes even clearer than it has been before
the sociological base of my position. More important, it highlights what
has perhaps not been clear before, the extent to which I regard scientific
knowledge as intrinsically a product of a congeries of specialists’ communi-
ties. Sir Karl sees ‘a great danger in . . . specialization’, and the context in
which he provides this evaluation suggests that the danger is the same one
he sees in normal science.’ But with respect to the former, at least, the

1 This volume, p. 53-

254 THOMAS 8S. KUHN

battle has clearly been lost from the start. Not that one might not wish for
good reasons to oppose specialization and even succeed in doing so, but
that the effort would necessarily be to oppose science as well. Whenever
Sir Karl contrasts science with philosophy, as he does at the start of his
paper, or physics with sociology, psychology, and history, as he does at the
end, he is contrasting an esoteric, isolated, and largely self-contained
discipline with one that still aims to communicate with and persuade an
audience larger than their own profession. (Science is not the only activity
the practitioners of which can be grouped into communities, but it is the
only one in which each community is its own exclusive audience and
judge.!) The contrast is not a new one, characteristic, say, of Big Science
and the contemporary scene. Mathematics and astronomy were esoteric
subjects in antiquity; mechanics became so after Galileo and Newton;
electricity after Coulomb and Poisson; and so on until economics today.
For the most part that transition to a closed specialists’ group was part of
the transition to maturity that I discussed above when considering the
emergence of puzzle solving. It is hard to believe that it is a dispensable
characteristic. Perhaps science could again become like philosophy, as Sir
Karl wishes, but I suspect that he would then admire it less.

To conclude this part of my discussion, I turn to some concrete cases by
means of which my critics illustrate their difficulties in finding normal
science and its functions in history, taking up first a problem raised by Sir
Karl and Watkins. Both point out that nothing like a consensus over
fundamentals ‘emerged during the long history of the theory of matter:
here from the pre-Socratics to the present day there has been an unending
debate between continuous and discontinuous concepts of matter, between
various atomic theories on the one hand, and ether, wave and field theories
on the other’.? Feyerabend makes a very similar point for the second half
of the nineteenth century by contrasting the mechanical, phenomenological
and field-theoretic approaches to problems of physics.? With all of their
descriptions of what went on I agree. But the term ‘theories of matter’
does not, at least until the last thirty years, even differentiate the concerns
of science from those of philosophy, much less single out a community or
small group of communities responsible for and expert in the subject.

I am not suggesting that scientists do not have and use theories of
matter, nor that their work is unaffected by such theories, nor that their
research results have no role in the theories of matter held by others. But

1 See my [1969].

2 This volume, pp. 34 ff, and 54-5. As Watkins notes, Dudley Shapere has made a similar
point in his [1964] in connection with the role of atomism in chemistry in the first half of
the nineteenth century. I deal with that case immediately below.

® This volume, p. 207.

REFLECTIONS ON MY CRITICS 255

until this century theories of matter have been a tool for scientists rather
than a subject matter. That different specialties have chosen different tools
and sometimes criticized each others’ choices does not mean that they have
not each been practising normal science. The frequently heard generaliza-
tion that, before the advent of wave mechanics, physicists and chemists
deployed characteristic and irreconcilable theories of matter is too sim-
plistic (partly because it can equally well be said about different chemical
specialties even today). But the very possibility of such a generalization
suggests the way in which the issue raised by Watkins and Sir Karl must
be approached. For that matter, the practitioners of a given community or
school need not always share a theory of matter. Chemistry during the
first half of the nineteenth century is a case in point. Though many of its
fundamental tools—constant proportion, multiple proportion, combining
weights, and so on—had been developed and become common property
through Dalton’s atomic theory, the men who used them could, after the
event, adopt widely varying attitudes about the nature and even the exis-
tence of atoms. Their discipline, or at least many parts of it, did not
depend upon a shared model for matter.

Even where they admit the existence of normal science, my critics
regularly have difficulty discovering crisis and its role. Watkins provides
an example, and its resolution follows at once from the sort of analysis
deployed above. Kepler’s Laws, Watkins reminds us, were incompatible
with Newton’s planetary theory, but astronomers had not previously been
dissatisfied with them. Newton’s revolutionary treatment of planetary
motions was not, Watkins therefore asserts, preceeded by astronomical
crisis. But why should it have been? In the first place, the transition from
Keplerian to Newtonian orbits need not have been (I lack the evidence to
be certain) a revolution for astronomers. Most of them followed Kepler and
explained the shape of the planetary orbits in mechanical rather than geo-
metrical terms. (Their explanation did not, that is, make use of the
ellipse’s ‘geometric perfection’, if any, or of some other characteristic
of which the orbit was deprived by Newtonian perturbations.) Though the
transition from circle to ellipse had been part of a revolution for them, a
minor adjustment of mechanism would account, as it did with Newton,
for departure from ellipticity. More important, Newton’s adjustment of
Keplerian orbits was a by-product of his work in mechanics, a field to
which the community of mathematical astronomers made passing reference
in their prefaces but which thereafter played only the most global role in
their work. In mechanics, however, where Newton did induce a revolution,
there had been a widely recognized crisis since the acceptance of Coper-
nicanism. Watkins’s counter-example is the best sort of grist for my mill.

256 THOMAS S. KUHN

I turn finally to one of Lakatos’s extended case histories, that of the
Bohr research programme, for it illustrates what most puzzles me about
his often admirable paper and suggests how deep even residual Popper-
ianism can be. Though his terminology is different, his analytic apparatus
is as close to mine as need be: hard core, work in the protective belt, and
degenerative phase are close parallels for my paradigms, normal science,
and crisis. Yet in important ways Lakatos fails to see how these shared
notions function even when applying them to what is for me an ideal case.
Let me illustrate some of the things he could have seen and might have
said. My version, like his or like any other bit of historical narrative, will
be a rational reconstruction. But I shall not ask my readers to apply ‘tons
of salt’ nor add footnotes pointing out that what is said in my text is
false.1

Consider Lakatos’s account of the origin of the Bohr atom. “The back-
ground problem’, he writes, ‘was the riddle of how Rutherford atoms...
can remain stable; for, according to the well-corroborated Maxwell-—
Lorentz theory of electromagnetism they should collapse.’ That is a
genuine Popperian problem (not a Kuhnian puzzle) arising from the
conflict between two increasingly well-established parts of physics. It had,
in addition, been available for some time as a potential focal point for
criticism. It did not originate with Rutherford’s model in 1911; radiative
instability was equally a difficulty for most older atom-models, including
both Thomson’s and Nagaoka’s. Furthermore, it is the problem which
Bohr (in some sense) solved in his famous three-part paper of 1913, thereby
inaugurating a revolution. No wonder Lakatos would like it to be the
‘background problem’ for the research programme that produced the revo-
lution, but it emphatically is not.$

Instead, the background was an entirely normal puzzle. Bohr set out to
improve the physical approximations in a paper by C. G. Darwin on the
energy lost by charged particles passing through matter. In the process he

1 This volume, pp. 138, 140 and 146, and elsewhere. One may reasonably ask about the
evidential force of examples that call for this sort of qualification (and is ‘qualification’ quite
the right word?). I shall, however, in another context be very grateful for these ‘case histories’
of Lakatos’s. More clearly, because more explicitly, than any other examples I know, they
illustrate the differences between the way philosophers and historians usually do history.
The problem is not that philosophers are likely to make errors—Lakatos knows the facts
better than many historians who have written on these subjects, and historians do make
egregious errors. But a historian would not include in his narrative a factual report which he
knew to be false. If he had done so, he would be so sensitive to the offence that he could
not conceivably compose a footnote calling attention to it. Both groups are scrupulous,
but they differ in what they are scrupulous about. I have discussed some differences of
this sort, in my unpublished Isenberg Lecture, ‘The Relations between History and

Philosophy of Science’, read in March 1968.
2 This volume, p. 141. 3 For what follows, see Heilbron and Kuhn [1969].

REFLECTIONS ON MY CRITICS 257

made what was to him the surprising discovery that the Rutherford atom,
unlike other current models, was mechanically unstable and that a Planck-
like ad hoc device for stabilizing it provided a promising explanation of the
periodicities in Mendeleev’s table, something else for which he had not
been looking. At that point his model still had no excited states, nor was
Bohr yet concerned to apply it to atomic spectra. Those steps followed,
however, as he attempted to reconcile his model with the apparently in-
compatible one developed by J. W. Nicholson and, in the process, en-
countered Balmer’s formula. Like much of the research that produces
revolutions, Bohr’s biggest achievements in 1913 were products, therefore,
of a research programme directed to goals very different from those
obtained. Though he could not have stabilized the Rutherford model by
quantization if unaware of the crisis which Planck’s work had introduced
to physics, his own work illustrates with particular clarity the revolutionary
efficacy of normal research puzzles.

Examine, finally, the concluding portion of Lakatos’s case history, the
degenerative phase of the old quantum theory. Most of the story he tells
well, and I shall simply point it up. From 1900 on it was increasingly
widely recognized among physicists that Planck’s quantum had introduced
a fundamental inconsistency into physics. At first many of them tried to
eliminate it, but, after 1911 and particularly after the invention of Bohr’s
atom, those critical efforts were increasingly abandoned. Einstein was, for
more than a decade, the only physicist of note who continued to direct his
energies towards the search for a consistent physics. Others learned to live
with inconsistency and tried instead to solve technical puzzles with the
tools at hand. Particularly in the areas of atomic spectra, atomic structure,
and specific heats, their achievements were unprecedented. Though the
inconsistency of physical theory was widely acknowledged, physicists could
nevertheless exploit it and by doing so made fundamental discoveries at an
extraordinary rate between 1913 and 1921. Quite suddenly, however,
beginning in 1922, these very successes were seen to have isolated three
obdurate problems—the helium model, the anomalous Zeeman effect, and
optical dispersion—which could not, physicists were increasingly con-
vinced, be resolved by anything quite like existing technique. As a result,
many of them changed their research stance, proliferating more and wilder
versions of the old quantum theory than before, designing and testing each
attempt against the three recognized trouble spots.

It is this last phase, 1922 and after, which Lakatos calls the degenerative
stage of Bohr’s programme. For me it is a case book example of crisis,
clearly documented in publications, correspondence, and anecdote. We
see it in very nearly the same way. Lakatos might therefore have told the

258 THOMAS 8, KUHN

rest of the story. To those who were experiencing this crisis, two of the
three problems which had provoked it proved immensely informative,
dispersion and the anomalous Zeeman effect. By a series of connected steps
too complex to be outlined here, their pursuit led first to the adoption in
Copenhagen of an atom model in which so-called virtual oscillators
coupled discrete quantum states, then to a formula for quantum-theore-
tical dispersion, and finally to matrix mechanics which terminated the
crisis barely three years after it had begun. For that first formulation of
quantum mechanics, the degenerative phase of the old quantum theory
provided both occasion and much detailed technical substance. History
of science, to my knowledge, offers no equally clear, detailed, and cogent
example of the creative functions of normal science and crisis.

Lakatos, however, ignores this chapter and jumps instead to wave
mechanics, the second and at first quite different formulation of a new
quantum theory. First, he describes the degenerative phase of the old
quantum theory as filled with ‘ever more sterile inconsistencies and ever
more ad hoc hypotheses’ (‘ad hoc’ and ‘inconsistencies’ are right; ‘sterile’
could not be more wrong; not only did these hypotheses lead to matrix
mechanics but also to electron spin). Then, he produces the crisis-resolving
innovation like a magician pulling a rabbit from a hat: ‘A rival research
programme soon appeared: wave mechanics... [which] soon caught up
with, vanquished and replaced Bohr’s programme. De Broglie’s paper came
at a time when Bohr’s programme was degenerating. But this was mere co-
incidence. One wonders what would have happened if de Broglie had
published his paper in 1914 instead of 1924.’

To the closing rhetorical question, the answer is clear: nothing at all.
Both de Broglie’s paper and the route from it to the Schrédinger wave
equation depend in detail on developments which occurred after 1914: on
work by Einstein and by Schrédinger himself as well as on the discovery of
the Compton effect in 1922.2 Even if that point could not be documented
in detail, however, is not coincidence strained beyond recognition when
used to explain the simultaneous emergence of two independent and at
first quite different theories, both capable of resolving a crisis that had
been visible for only three years?

Let me be scrupulous. Though Lakatos entirely misses the essential
creative functions of the crisis of the old quantum theory, he is not altogether
wrong about its relevance to the invention of wave mechanics. The wave
equation was not a response to the crisis which began in 1922 but to the
one which dates from Planck’s work in 1900 and on which most physicists
had turned their backs after 1911. If Einstein had not tenaciously refused to

1 This volume, p. 154; my italics. ? See Klein [1964] and Raman and Ferman [1969].

REFLECTIONS ON MY CRITICS 259

set aside his deep dissatisfaction with the fundamental inconsistencies of
the old quantum theory (and if he had not been able to attach that dis-
content to the concrete technical puzzles of electromagnetic fluctuation
phenomena—something for which he found no equivalent after 1925),
the wave equation would not have emerged when and as it did. The re-
search route which leads to it is not the same as the route to matrix mech-
anics.

But neither are the two independent, nor is the simultaneity of their
termination due merely to coincidence. Among the several research
episodes which tie them together is, for example, Compton’s convincing
demonstration in 1922 of the particulate properties of light, the by-
product of a very high-class piece of normal research on X-ray scattering.
Before physicists could consider the idea of matter waves, they had first to
take the idea of the photon seriously, and this few of them had done
before 1922. De Broglie’s work started as photon theory, its main thrust
being to reconcile Planck’s radiation law with the particulate structure of
light; matter waves entered along the way. De Broglie himself may not
have needed Compton’s discovery in order to take the photon seriously,
but his audience, French and foreign, certainly did. Though wave mech-
anics in no sense follows from the Compton effect, there are historical ties
between the two. On the road to matrix mechanics the role of the Compton
effect is even clearer. The first use of the virtual oscillator model in Copen-
hagen was to show how that effect could be explained without recourse to
Einstein’s photon, a concept that Bohr had been notoriously reluctant to
accept. The same model was next applied to dispersion and the clues to
matrix mechanics found. The Compton effect is therefore one bridge
across the gap which Lakatos hides under ‘coincidence’.

Having provided elsewhere many other examples of the significant roles
of normal science and crisis, I shall not multiply them further here. For
lack of additional research I could not, in any case, provide enough. When
completed, that research need not bear me out, but what has been done so
far surely fails to support my critics. They must look further for counter-
examples.

5. IRRATIONALITY AND THEORY-CHOICE

I consider now one last set of concerns voiced by my present critics, in
this case one they share with a number of other philosophers. It arises
mainly from my description of the procedures by which scientists choose
between competing theories, and it results in charges which cluster about
such terms as ‘irrationality’, ‘mob rule’, and ‘relativism’. In this section J
aim to eliminate misunderstandings for which my own past rhetoric is

260 THOMAS Ss. KUHN

doubtless partially responsible. In my concluding section, which follows, I
shall touch upon some deeper issues raised by the problem of theory—
choice. At that point the terms ‘paradigm’ and ‘incommensurability’,
which I have so far almost entirely avoided, will necessarily re-enter the
discussion.

In my Scientific Revolutions normal science is at one point described as

‘a strenuous and devoted attempt to force nature into the conceptual boxes
supplied by professional education.’ Later, discussing the problems which
surround the choice between competing sets of boxes, theories, or para-
digms, I described them as?:
about techniques of persuasion, or about argument and counter argument in a
situation in which . . . neither proof nor error is at issue. The transfer of allegiance
from paradigm to paradigm is a conversion experience that cannot be forced.
Lifelong resistance .. . is not a violation of scientific standards but an index to the
nature of scientific research itself... . Though the historian can always find men—
Priestley, for instance—who were unreasonable to resist for as long as they did,
he will not find a point at which resistance becomes illogical or unscientific. At
most he may wish to say that the man who continues to resist after his whole pro-
fession has been converted has ipso facto ceased to be a scientist.
Not surprisingly (though I have myself been very much surprised), pas-
sages like these are in some quarters read as implying that, in the de-
veloped sciences, might makes right. Members of a scientific community
can, I am held to have claimed, believe anything they please if only they will
first decide what they agree about and then enforce it both on their col-
leagues and on nature. The factors whith determine what they do choose to
believe are fundamentally irrational, matters of accident and personal
taste. Neither logic nor observation nor good reason is implicated in
theory—choice. Whatever scientific truth may be, it is through-and-through
relativistic,

These are all damaging misinterpretations, whatever my responsibility
may be for making them possible. Though their elimination will still leave
a deep divide between my critics and me, it is prerequisite even to dis-
covering our disagreement. Before treating them individually, however,
one general remark should be helpful. The sorts of misinterpretations just
outlined are voiced only by philosophers, a group already familiar with the
points at which I aim in passages like the above. Unlike readers to whom
the point is less familiar, they sometimes suppose that I intend more than I
do. What I mean to be saying, however, is only the following.

In a debate over choice of theory, neither party has access to an argu-
ment which resembles a proof in logic or formal mathematics. In the latter,
both premises and rules of inference are stipulated in advance. If there

1Cf. my [1962a], p. 5. 2 Op. cit. p. 151.

REFLECTIONS ON MY CRITICS 261

is disagreement about conclusions, the parties to the debate can retrace
their steps one by one, checking each against prior stipulation. At the end
of that process, one or the other must concede that at an isolable point in
the argument he has made a mistake, violated or misapplied a previously
accepted rule. After that concession he has no recourse, and his opponent’s
proof is then compelling. Only if the two discover instead that they differ
about the meaning or applicability of a stipulated rule, that their prior
agreement does not provide a sufficient basis for proof, does the ensuing
debate resemble what inevitably occurs in science.

Nothing about this relatively familiar thesis should suggest that scientists
do not use logic (and mathematics) in their arguments, including those
which aim to persuade a colleague to renounce a favoured theory and
embrace another. I am dumbfounded by Sir Karl’s attempt to convict me
of self-contradiction because I employ logical arguments myself.1 What
might better be said is that I do not expect that, merely because my argu-
ments are logical, they will be compelling. Sir Karl underscores my point,
not his, when he describes them as logical but mistaken, and then makes
no attempt to isolate the mistake or to display its logical character. What he
means is that, though my arguments are logical, he disagrees with my con-
clusion. Our disagreement must be about premises or the manner in which
they are to be applied, a situation which is standard among scientists
debating theory-choice. When it occurs, their recourse is to persuasion as a
prelude to the possibility of proof.

To name persuasion as the scientist’s recourse is not to suggest that
there are not many good reasons for choosing one theory rather than
another.” It is emphatically not my view that ‘adoption of a new scientific
theory is an intuitive or mystical affair, a matter for psychological descrip-
tion rather than logical or methodological codification’. On the contrary,
the chapter of my Scientific Revolutions from which the preceding quota-
tion was abstracted explicitly denies ‘that new paradigms triumph ulti-
mately through some mystical aesthetic’, and the pages which precede that
denial contain a preliminary codification of good reasons for theory
choice.* These are, furthermore, reasons of exactly the kind standard in
philosophy of science: accuracy, scope, simplicity, fruitfulness, and the
like. It is vitally important that scientists be taught to value these character-
istics and that they be provided with examples that illustrate them in
practice. If they did not hold values like these, their disciplines would

1 This volume, pp. §§ and 57.

® For one version of the view that Kuhn insists that ‘the decisions of a scientific group to
adopt a new paradigm cannot be based on good reasons of any kind, factual or otherwise’,

see Shapere [1966], especially p. 67.

3 Cf, Scheffler [1967], p. 18. 4 Cf. my [1962a], p. 157.

262 THOMAS S. KUHN

develop very differently. Note, for example, that the periods in which the
history of art was a history of progress were also the periods in which the
artist’s aim was accuracy of representation. With the abandonment of that
value, the developmental pattern changed drastically though very signi-
ficant development continued.

What I am denying then is neither the existence of good reasons nor
that these reasons are of the sort usually described. I am, however, in-
sisting that such reasons constitute values to be used in making choices
rather than rules of choice. Scientists who share them may nevertheless
make different choices in the same concrete situation. Two factors are
deeply involved. First, in many concrete situations, different values,
though all constitutive of good reasons, dictate different conclusions,
different choices. In such cases of value-conflict (e.g. one theory is simpler
but the other is more accurate) the relative weight placed on different
values by different individuals can play a decisive role in individual
choice. More important, though scientists share these values and must
continue to do so if science is to survive, they do not all apply them in the
same way. Simplicity, scope, fruitfulness, and even accuracy can be judged
quite differently (which is not to say they may be judged arbitrarily)
by different people. Again, they may differ in their conclusions without
violating any accepted rule.

That variability of judgement may, as I suggested above in connection
with the recognition of crises, even be essential to scientific advance. The
choice of a theory, which is, as Lakatos says, equally the choice of a re-
search programme, involves major risks, particularly in its early stages.
Some scientists must, by virtue of a value system differing in its applica-
bility from the average, choose it early, or it will not be developed to the
point of general persuasiveness. The choices dictated by these atypical
value systems are, however, generally wrong. If all members of the com-
munity applied values in the same high-risk way, the group’s enterprise
would cease. This last point, I think, Lakatos misses, and with it the
essential role of individual variability in what is only belatedly the unani-
mous decision of the group. As Feyerabend also emphasizes, to give these
decisions a ‘historical character’ or to suggest that they are made only ‘with
hindsight’ deprives them of their function.2 The scientific community
cannot wait for history, though some individual members do. The needed
results are instead achieved by distributing the risk that must be taken
among the group’s members.

Does anything in this argument suggest the appropriateness of phrases

1 Gombrich, [1960], pp. 11 f.
2 This volume, pp. 120 and 215 ff.

REFLECTIONS ON MY CRITICS 263

like decision by ‘mob psychology’?! I think not. On the contrary, one
characteristic of a mob is its rejection of values which its members ordi-
narily share. Done by scientists, the result should be the end of their
science, and the Lysenko case suggests that it would be. My argument,
however, goes even further, for it emphasizes that, unlike most disciplines,
the responsibility for applying shared scientific values, must be left to the
specialists’ group.? It may not even be extended to all scientists, much less
to all educated laymen, much less to the mob. If the specialists’ group
behaves as a mob, renouncing its normal values, then science is already
past saving.

By the same token, no part of the argument here or in my book implies
that scientists may choose any theory they like so long as they agree in
their choice and thereafter enforce it.2 Most of the puzzles of normal
science are directly presented by nature, and all involve nature indirectly.
Though different solutions have been received as valid at different times,
nature cannot be forced into an arbitrary set of conceptual boxes. On the
contrary, the history of proto-science shows that normal science is possible
only with very special boxes, and the history of developed science shows
that nature will not indefinitely be confined in any set which scientists
have constructed so far. If Isometimes say that any choice made by scientists
on the basis of their past experience and in conformity with their tradi-
tional values is ipso facto valid science for its time, I am only underscoring
a tautology. Decisions made in other ways or decisions that could not be
made in this way provide no basis for science and would not be scientific.

The charges of irrationality and relativism remain. To the first, however,
I have already spoken, for I have discussed the issues, excepting incom-
mensurability, from which it seems to arise. I am not sanguine in this
matter, however, for I have not previously and do not now understand
quite what my critics mean when they employ terms like ‘irrational’ and
‘irrationality’ to characterize my views. These labels seem to me mere
shibboleths, barriers to a joint enterprise whether conversation or research.
My difficulties in understanding are, however, even clearer and more
acute when these terms are used not to criticize my position but in its
defence. Obviously there is much in the last part of Feyerabend’s paper with

1 This volume, pp. 140, footnote 3, and 178.

2 Cf. my [{1962a], p. 167.

3 Some sense of my surprise and chagrin over this and related ways of reading my book
may be generated by the following anecdote. During a meeting I was talking to a usually
far-distant friend and colleague whom I knew, from a published review, to be enthusiastic
about my book. She turned to me and said, ‘Well, Tom, it seems to me that your biggest
problem now is showing in what sense science can be empirical’. My jaw dropped and still
sags slightly. I have total visual recall of that scene and of no other since de Gaulle’s entry
into Paris in 1944.

264 THOMAS S. KUHN

which I agree, but to describe the argument as a defence of irrationality in
science seems to me not only absurd but vaguely obscene. I would de-
scribe it, together with my own, as an attempt to show that existing
theories of rationality are not quite right and that we must readjust or
change them to explain why science works as it does. To suppose, instead,
that we possess criteria of rationality which are independent of our under-
standing of the essentials of the scientific process is to open the door to
cloud-cuckoo land.

An answer to the charge of relativism must be more complex than those
which precede, for the charge arises from more than misunderstanding.
In one sense of the term I may be a relativist; in a more essential one I am
not. What I can hope to do here is separate the two. It must already be
clear that my view of scientific development is fundamentally evolutionary.
Imagine, therefore, an evolutionary tree representing the development of
the scientific specialties from their common origin in, say, primitive nat-
ural philosophy. Imagine, in addition, a line drawn up that tree from the
base of the trunk to the tip of some limb without doubling back on itself.
Any two theories found along this line are related to each other by descent.
Now consider two such theories, each chosen from a point not too near
its origin fT believe it would be easy to design a set of criteria—including
maximum accuracy of predictions, degree of specialization, number (but
not scope) of concrete problem solutions—which would enable any
observer involved with neither theory to tell which was the older, which the
descendant. For me, therefore, scientific development is, like biological
evolution, unidirectional and irreversible.\One scientific theory is not as
good as another for doing what scientists normally do. In that sense I am
not a relativist.

But there are reasons why I get called one, and they relate to the con-
texts in which J am wary about applying the label ‘truth’. In the present
context, its intra-theoretic uses seem to me unproblematic. Members of a
given scientific community will generally agree which consequences of a
shared theory sustain the test of experiment and are therefore true, which
are false as theory is currently applied, and which are as yet untested.
Dealing with the comparison of theories designed to cover the same range
of natural phenomena, I am more cautious. If they are historical theories,
like those considered above, I can join Sir Karl in saying that each was
believed to be true in its time but was later abandoned as false. In addition,
I can say that the later theory was the better of the two as a tool for the
practice of normal science, and I can hope to add enough about the senses
in which it was better to account for the main developmental character-
istics of the sciences. Being able to go that far, I do not myself feel that I

REFLECTIONS ON MY CRITICS 265

am a relativist. Nevertheless, there is another step, or kind of step, which
many philosophers of science wish to take and which I refuse. They wish,
that is, to compare theories as representations of nature, as statements
about ‘what is really out there’. Granting that neither theory of a historical
pair is true, they nonetheless seek a sense in which the later is a better
approximation to the truth. I believe nothing of that sort can be found. On
the other hand, I no longer feel that anything is lost, least of all the ability
to explain scientific progress, by taking this position.

What I am rejecting will be clarified by reference to Sir Karl’s paper and
to his other writings. He has proposed a criterion of verisimilitude which
permits him to write that ‘a later theory... t, has superseded ¢,... by
approaching more closely to the truth than ¢,’. Also, when discussing a suc-
cession of frameworks, he speaks of each later member of the series as
‘better and roomier’ than its predecessors; and he implies that the limit of
the series, at least if carried to infinity, is ‘ “absolute” or “objective” truth,
in Tarski’s sense’.1 Those positions present, however, two problems, about
the first of which I am uncertain of Sir Karl’s position. To say, for example,
of a field theory that it ‘approach[es] more closely to the truth’ than an
older matter-and-force theory should mean, unless words are. being oddly
used, that the ultimate constituents of nature are more like fields than like
matter and force. But in this ontological context it is far from clear how the
phrase ‘more like’ is to be applied. Comparison of historical theories gives
no sense that their ontologies are approaching a limit: in some funda-
mental ways Einstein’s general relativity resembles Aristotle’s physics
more than Newton’s. In any case, the evidence from which conclusions
about an ontological limit are to be drawn is the comparison not of whole
theories but of their empirical consequences. That is a major leap, par-
ticularly in the face of a theorem that any finite set of consequences of a
given theory can be derived from another incompatible one.

The other difficulty is highlighted by Sir Karl’s reference to Tarski and
is more fundamental. The semantic conception of truth is regularly
epitomized in the example: ‘Snow is white’ is true if and only if snow is
white. To apply that conception in the comparison of two theories, one
must therefore suppose that their proponents agree about technical equiva-
lents of such matters of fact as whether snow is white. If that supposition
were exclusively about objective observation of nature, it would present no
insuperable problems, but it involves as well the assumption that the
objective observers in question understand ‘snow is white’ in the same way,
a matter which may not be obvious if the sentence reads ‘elements combine
in constant proportion by weight’. Sir Karl takes it for granted that the

1 Popper [1963], chapter 10, particularly p. 232; and this volume, p. 56; my italics,

266 THOMAS Ss. KUHN

proponents of competing theories do share a neutral language adequate to
the comparision of such observation reports. I am about to argue that
they do not. If I am right, then ‘truth’ may, like ‘proof’, be a term with
only intra-theoretic applications. Until this problem of a neutral observa-
tion language is resolved, confusion will only be perpetuated by those who
point out (as Watkins does when responding to my closely parallel re-
marks about ‘mistakes’) that the term is regularly used as though the
transfer from intra- to inter-theoretic contexts made no difference.

6. INCOMMENSURABILITY AND PARADIGMS

At last we arrive at the central constellation of issues which separate me
from most of my critics. I regret the length of the journey to this point but
accept only partial responsibility for the brush that has had to be cleared
from the path. Unfortunately, the necessity of relegating these issues to my
concluding section results in a relatively cursory and dogmatic treatment.
I can hope only to isolate some aspects of my viewpoint which my critics
have generally missed or dismissed and to provide motives for further
reading and discussion.

The point-by-point comparison of two successive theories demands a
language into which at least the empirical consequences of both can be
translated without loss or change. That such a language lies ready to hand
has been widely assumed since at least the seventeenth century when
philosophers took the neutrality of pure sensation-reports for granted and
sought a ‘universal character’ which would display all languages for ex-
pressing them as one. Ideally the primitive vocabulary of such a language
would consist of pure sense-datum terms plus syntactic connectives.
Philosophers have now abandoned hope of achieving any such ideal, but
many of them continue to assume that theories can be compared by re-
course to a basic vocabulary consisting entirely of words which are attached
to nature in ways that are unproblematic and, to the extent necessary,
independent of theory. That is the vocabulary in which Sir Karl’s basic
statements are framed. He requires it in order to compare the verisimili-
tude of alternate theories or to show that one is ‘roomier’ than (or includes)
its predecessor. Feyerabend and I have argued at length that no such
vocabulary is available. In the transition from one theory to the next
words change their meanings or conditions of applicability in subtle ways.”

1 This volume, p. 26, footnote 3.

2 In his [1964], Shapere criticizes, in part quite properly, the way I discuss meaning-
change in my book, In the process he challenges me to specify the ‘cash difference’ between a
change in meaning and an alteration in the application of a term. Need I say that, in the
present state of the theory of meaning, there is none. The identical point can be made using
either term,

REFLECTIONS ON MY CRITICS 267

Though most of the same signs are used before and after a revolu-
tion—e.g. force, mass, element, compound, cell—the ways in which some
of them attach to nature has somehow changed. Successive theories are
thus, we say, incommensurable.

Our choice of the term ‘incommensurable’ has bothered a number of
readers. Though it does not mean ‘incomparable’ in the field from which
it was borrowed, critics have regularly insisted that we cannot mean it
literally since men who hold different theories do communicate and some-
times change each others’ views. More important, critics often slide from
the observed existence of such communication, which I have underscored
myself, to the conclusion that it can present no essential problems. Toul-
min seems content to admit ‘conceptual incongruities’ and then go on as
before.? Lakatos inserts parenthetically the phrase ‘or from semantical
reinterpretations’ when telling us how to compare successive theories and
thereafter treats the comparison as purely logical.? Sir Karl exorcises the
difficulty in a way that has particular interest: ‘It is just a dogma—a
dangerous dogma—that the different frameworks are like mutually un-
translatable languages. The fact is that even totally different languages
(like English and Hopi, or Chinese) are not untranslatable, and that there
are many Hopis or Chinese who have learnt to master English very
well.’4

I accept the utility, indeed the importance, of the linguistic parallel,
and shall therefore dwell for a bit upon it. Presumably Sir Karl accepts it
too since he uses it. If he does, the dogma to which he objects is not that
frameworks are like languages but that languages are untranslatable. But
no one ever believed they were! What people have believed, and
what makes the parallel important, is that the difficulties of learning a
second language are different from and far less problematic than the
difficulties of translation. Though one must know two languages in order
to translate at all, and though translation can then always be managed up
to a point, it can present grave difficulties to even the most adept bilingual.
He must find the best available compromises between incompatible
objectives. Nuances must be preserved but not at the price of sentences so
long that communication breaks down. Literalness is desirable but not if
it demands introducing too many foreign words which must be separately
discussed in a glossary or appendix. People deeply committed both to
accuracy and to felicity of expression find translation painful, and some
cannot do it at all.

1 See, for example, this volume, pp. 43-4. 2 This volume, p. 44.

3 This volume, p. 118. Perhaps only because of its excessive brevity, Lakatos’s other
reference to this problem on p. 179, note 1, is equally little helpful.

4 This volume, p. 56.

268 THOMAS S. KUHN

Translation, in short, always involves compromises which alter com-
munication. The translator must decide what alterations are acceptable.
To do that he needs to know what aspects of the original it is most impor-
tant to preserve and also something about the prior education and exper-
ience of those who will read his work. Not surprisingly, therefore, it is
today a deep and open question what a perfect translation would be and
how nearly an actual translation can approach the ideal. Quine has recently
concluded ‘that rival systems of analytic hypotheses [for the preparation
of translations] can conform to all speech dispositions within each of the
languages concerned and yet dictate, in countless cases, utterly disparate
translation ... Two such translations might even be patently contrary in
truth value.’t One need not go that far to recognize that reference to
translation only isolates but does not resolve the problems which have led
Feyerabend and me to talk of incommensurability. To me at least, what
the existence of translations suggests is that recourse is available to scien-
tists who hold incommensurable theories. That recourse need not, how-
ever, be to full restatement in a neutral language of even the theories’
consequences. The problem of theory-comparison remains.

Why is translation, whether between theories or languages, so difficult?
Because, as has often been remarked, languages cut up the world in
different ways, and we have no access to a neutral sub-linguistic means of
reporting. Quine points out that, though the linguist engaged in radical
translation can readily discover that his native informant utters ‘Gavagai’
because he has seen a rabbit, it is more difficult to discover how ‘Gavagai’
should be translated. Should the linguist render it as ‘rabbit’, ‘rabbit-kind’,
‘rabbit-part’, ‘rabbit-occurrence’, or by some other phrase he may not
even have thought to formulate? I extend the example by supposing that,
in the community under examination, rabbits change colour, length of
hair, characteristic gait, and so on during the rainy season, and that their
appearance then elicits the term ‘Bavagai’. Should ‘Bavagai’ be trans-
lated ‘wet rabbit’, ‘shaggy rabbit’, limping rabbit’, all of these together, or
should the linguist conclude that the native community has not recognized
that ‘Bavagai’ and ‘Gavagai’ refer to the same animal? Evidence relevant
to a choice among these alternatives will emerge from further investiga-
tion, and the result will be a reasonable analytic hypothesis with implica-
tion for the translation of other terms as well. But it will be only a hypo-
thesis (none of the alternatives considered above need be right); the result
of any error may be later difficulties in communication; when it occurs, it
will be far from clear whether the problem is with translation and, if so,
where the root difficulty lies.

_ ? Quine [1960], pp. 73 ff.

REFLECTIONS ON MY CRITICS 269

These examples suggest that a translation manual inevitably embodies a
theory, which offers the same sorts of reward, but also is prone to the same
hazards, as other theories. To me they also suggest that the class of trans-
lators includes both the historian of science and the scientist trying to
communicate with a colleague who embraces a different theory.! (Note,
however, that the motives and correlated sensitivities of the scientists and
historian are very different, which accounts for many systematic differences
in their results.) They often have the inestimable advantage that the signs
used in the two languages are identical or nearly so, that most of them
function the same way in both languages, and that, where function has
changed, there are neve.theless informative reasons for retaining the same
sign. But those advantages bring with them penalties illustrated in both
scientific discourse and history of science. They make it excessively easy
to ignore functional changes that would be apparent if they had been
accompanied by a change of sign.

The parallel between the task of the historian and the linguist highlights
an aspect of translation with which Quine does not deal (he need not) and
that has made trouble for linguists.2 Teaching Aristotelian physics to
students, I regularly point out that matter (in the Physics, not the Meta-
physics), just because of its omnipresence and qualitative neutrality, is a
physically dispensable concept. What populates the Aristotelian universe,
accounting for both its diversity and regularity, is immaterial ‘natures’ or
‘essences’; the appropriate parallel for the contemporary periodic table is
not the four Aristotelian elements, but the quadrangle of four fundamental
forms. Similarly, when teaching the development of Dalton’s atomic
theory, I point out that it implied a new view of chemical combination
with the result that the line separating the referents of the terms ‘mixture’
and ‘compound’ shifted; alloys were compounds before Dalton, mixtures
after.3 Those remarks are part and parcel of my attempt to translate older
theories into modern terms, and my students characteristically read source
materials, though already rendered into English, differently after I have

1 A number of these ideas about translation were developed in my Princeton seminar.
I cannot now distinguish my contributions from those of the students and colleagues who
attended. A paper by Tyler Burge was, however, particularly helpful.

2 See particularly Nida [1964]. I am much indebted to Sarah Kuhn for calling this
paper to my attention.

3 This example makes particularly clear the inadequacy of Scheffler’s suggestion that
the problems raised by Feyerabend and me vanish if one substitutes sameness-of-reference
for sameness-of-meaning (Scheffler [1967], chapter 3). Whatever the reference of ‘compound’
may be, in this example it changes. But, as the following discussion will indicate, sameness-
of-reference is no more free of difficulty than sameness-of-meaning in any of the applica-
tions that concern me and Feyerabend. Is the referent of ‘rabbit’ the same as that of ‘rabbit-
kind’ or of ‘rabbit-occurrence’? Consider the criteria of individuation and of self-identity
which fit each of the terms.

270 THOMAS S. KUHN

made them than they did before. By the same token, a good translation
manual, particularly for the language of another region and culture,
should include or be accompanied by discursive paragraphs explaining
how native speakers view the world, what sorts of ontological categories
they deploy. Part of learning to translate a language or a theory is learning
to describe the world with which the language or theory functions.

Having introduced translation to illustrate the illumination that can be
had by regarding scientific communities as language communities, I now
leave it for a time in order to examine a particularly important aspect of
the parallelism. In learning either a science or a language, vocabulary is
generally acquired together with at least a minimal battery of generaliza-
tions which exhibit it applied to nature. In neither case, however, do the
generalizations embody more than a fraction of the knowledge of nature
which has been acquired in the learning process. Much of it is embodied
instead in the mechanism, whatever it may be, which is used to attach
terms to nature. Both natural and scientific language are designed to
describe the world as it is, not any conceivable world. The former, it is
true, adapts to the unexpected occurrence more easily than the latter, but
often at the price of long sentences and dubious syntax. Things which
cannot readily be said in a language are things that its speakers do not
expect to have occasion to say. If we forget this or underestimate its import-
ance, that is probably because its converse does not hold. We can readily
describe many things (unicorns, for example) which we do not expect
to see.

How, then, do we acquire the knowledge of nature that is built into
language? For the most part by the same techniques and at the same time
as we acquire language itself, whether everyday or scientific. Parts of the
process are well known. The definitions in a dictionary tell us something
about what words mean and simultaneously inform us of the objects and
situations about which we may need to read or speak. About some of these
words we learn more, and about others everything we know, by encounter-
ing them in a variety of sentences. Under those circumstances, as Carnap
has shown, we acquire laws of nature together with a knowledge of mean-
ings. Given a verbal definition of two tests, each definitive, for the presence
of an electric charge, we learn both about the term ‘charge’ and also that a
body which passes one test will also pass the other. These procedures for
language-nature learning are, however, purely linguistic. They relate
words to other words and thus can function only if we already possess some
vocabulary acquired by a non-verbal or incompletely verbal process.

1 For an extended example, see my [1964]. A more analytic discussion will be found in
my [1970].

REFLECTIONS ON MY CRITICS 271

Presumably that part of learning is by ostension or some elaboration of it,
the direct matching of whole words or phrases to nature. If Sir Karl and I
have a fundamental philosophic dispute, it is about the relevance of this
last mode of language-nature learning to philosophy of science. Though he
knows that many words needed by scientists, particularly for the formula-
tion of basic sentences, are learned by a process not fully linguistic, he
treats those terms and the knowledge acquired with them as unproblem-
atic, at least in the context of theory-choice. I believe he misses a central
point, the one which led me to introduce the notion of paradigms in my
Scientific Revolutions.

When I speak of knowledge embedded in terms and phrases learned by
some non-linguistic process like ostension, I am making the same point
that my book aimed to make by repeated reference to the role of paradigms
as concrete problem solutions, the exemplary objects of an ostension. When
I speak of that knowledge as consequential for science and for theory-con-
struction, I am identifying what Miss Masterman underscores about
paradigms by saying that they ‘can function when the theory is not
there’.! These ties are not, however, likely to be apparent to anyone who
has taken the notion of paradigm less seriously than Miss Masterman,
for, as she quite properly emphasizes, I have used the term in a number of
different ways. To discover what is presently the issue, I must briefly
digress to unravel confusions, in this case ones that are entirely of my own
making.

In Section 4, above, I remarked that a new version of my Scientific
Revolutions would open with a discussion of community structure. Having
isolated an individual specialists’ group, I would next ask what its mem-
bers shared that enabled them to solve puzzles and that accounted for their
relative unanimity in problem-choice and in the evaluation of problem-
solutions. One answer which my book licences to that question is ‘a
paradigm’ or ‘a set of paradigms’. (This is Miss Masterman’s sociological
sense of the term.) For it I should now like some other phrase, perhaps
‘disciplinary matrix’: ‘disciplinary’, because it is common to the prac-
titioners of a specified discipline; ‘matrix’, because it consists of ordered
elements which require individual specification. All of the objects of com-
mitment described in my book as paradigms, parts of paradigms, or para-
digmatic would find a place in the disciplinary matrix, but they would not
be lumped together as paradigms, individually or collectively. Among
them would be: shared symbolic generalizations, like ‘f = ma’, or ‘elements
combine in constant proportion by weight’; shared models, whether meta-
physical, like atomism, or heuristic, like the hydrodynamic model of the

1 This volume p. 66.

272 THOMAS S. KUHN

electric circuit; shared values, like the emphasis on accuracy of prediction,
discussed above; and other elements of the sort. Among the latter I would
particularly emphasize concrete problem solutions, the sorts of standard
examples of solved problems which scientists encounter first in student
laboratories, in the problems at the ends of chapters in science texts, and on
examinations. If I could, I would call these problem-solutions paradigms,
for they are what led me to the choice of the term in the first place. Having
lost control of the word, however, I shall henceforth describe them as
exemplars.?

Ordinarily problem-solutions of this sort are viewed as mere applica-
tions of theory that has already been learned. The student does them for
practice, to gain facility in the use of what he already knows. Undoubtedly
that description is correct after enough problems have been done, but
never, I think, at the start. Rather, doing problems is learning the language
of a theory and acquiring the knowledge of nature embedded in that
language. In mechanics, for example, many problems involve applications
of Newton’s Second Law, usually stated as ‘f = ma.’ That symbolic
expression is, however, a law-sketch rather than a law. It must be rewritten
in a different symbolic form for each physical problem before logical and
mathematical deduction are applied to it. For free fall it becomes

2 2
mg = mes for the pendulum it is mg Sin 6 = — mls; for coupled har-
monic oscillators it becomes two equations, the first of which may be

2
written m+ hy Ss, = k,(d+s.—s,); and so on.

Lacking space to develop an argument, I shall simply assert that physi-
cists share few rules, explicit or implicit, by which they make the transition
from law-sketch to the specific symbolic forms demanded by individual

1 This modification and almost everything else in the remainder of this paper is discussed
in far more detail and with more evidence in my [1970]. I refer readers to it even for biblio-
graphical references. One additional remark is, however, in place here. The change just
outlined in my text deprives me of recourse to the phrases ‘pre-paradigm period’ and ‘post-
paradigm period’ when describing the maturation of a scientific specialty. In retrospect
that seems to me all to the good, for, in both senses of the term, paradigms have throughout
been possessed by any scientific community, including the schools of what I previously
called the ‘pre-paradigm period’. My failure to see that point earlier has certainly helped
to make a paradigm seem a quasi-mystical entity or property that, like charisma, trans-
forms those infected by it. Note, however, as Section 3 indicates, that this alteration in
terminology does not at all alter my description of the maturation process. The early
stages in the development of most sciences are characterized by the presence of a number
of competing schools. Later, usually in the aftermath of a notable scientific achievement,
all or most of these schools vanish, a change which permits a far more powerful professional
behaviour to the members of the remaining community. On this whole problem, Miss
Masterman’s remarks (above, pp. 70-72) seem to me very telling.

REFLECTIONS ON MY CRITICS 273

problems. Instead, exposure to a series of exemplary problem-solutions
teaches them to see different physical situations as like each other; they are,
if you will, seen in a Newtonian gestalt. Once students have acquired the
ability to see a number of problem-situations in that way, they can write
down ad lib the symbolic forms demanded by other such situations as they
arise. Before that acquisition, however, Newton’s Second Law was to
them little or no more than a string of uninterpreted symbols. Though
they shared it, they did not know what it meant and it therefore told them
little about nature. What they had yet to learn was not, however, embodied
in additional symbolic formulations. Rather it was gained by a process
like ostension, the direct exposure to a series of situations each of which,
they were told, were Newtonian.

Seeing problem-situations as like each other, as subjects for the appli-
cation of similar techniques, is also an important part of normal scientific
work. One example may both illustrate the point and drive it home.
Galileo found that a ball rolling down an incline acquires just enough
velocity to return it to the same vertical height on a second incline of any
slope, and he learned to see that experimental situation as like the pend-
ulum with a point-mass for a bob. Huyghens then solved the problem of
the centre of oscillation of a physical pendulum by imagining that the
extended body of the latter was composed of Galilean point-pendula, the
bonds between which could be released at any point in the swing. After
the bonds were released, the individual point-pendula would swing freely,
but their collective centre of gravity, when each was at its highest point,
would be only at the height from which the centre of gravity of the extended
pendulum had begun to fall. Finally, Daniel Bernoulli, still with no aid
from Newton’s Laws, discovered how to make the flow of water from an
orifice in a storage tank resemble Huyghens’s pendulum. Determine the
descent of the centre of gravity of the water in tank and jet during an
infinitesimal period of time. Next imagine that each particle of water after-
wards moves separately upward to the maximum height obtainable with
the velocity it possessed at the end of the interval of descent. ‘The ascent
of the centre of gravity of the separate particles must then equal the
descent of the centre of gravity of the water in tank and jet. From that view
of the problem the long sought speed of efflux followed at once. These
examples display what Miss Masterman has in mind when she speaks of a
paradigm as fundamentally an artefact which transforms problems to
puzzles and enables them to be solved even in the absence of an adequate
body of theory.

Is it clear that we are back to language and its attachment to nature? Only
one law was used in all of the preceding examples. Known as the Principle

274 THOMAS S. KUHN

of wis viva, it was generally stated as ‘Actual descent equals potential
ascent’. Contemplating the examples is an essential part (though only
part) of learning what the words in that law mean individually and collec-
tively, or in learning how they attach to nature. Equally, it is part of learn-
ing how the world behaves. ‘The two cannot be separated. The same double
role is played by the textbook problems from which students learn, for
example, to discover forces, masses, accelerations in nature and in the
process find out what ‘f = ma’ means and how it attaches to and legislates
for nature. In none of these cases do the examples function alone, of
course. The student must know mathematics, some logic, and above all
natural language and the world to which it applies. But the latter pair has
to a considerable extent been learned in the same way, by a series of
ostensions which have taught him to see mother as always like herself and
different from father and sister, which have taught him to see dogs as
similar to each other and unlike cats, and so on. These learned similarity-
dissimilarity relationships are ones that we all deploy every day, unprob-
lematically, yet without being able to name the characteristics by which we
make the identifications and discriminations. They are prior, that is, to a
list of criteria which, joined in a symbolic generalization, would enable us
to define our terms. Rather they are parts of a language-conditioned or
language-correlated way of seeing the world. Until we have acquired them,
we do not see a world at all.

For a more leisurely and developed account of this aspect of the language-
theory parallel, I shall have to refer readers to the previously cited paper
from which much in the last few paragraphs is abstracted. Before re-
turning to the problem of theory-choice, however, I must at least state the
point which that paper primarily aims to defend. When I speak of learning
language and nature together by ostension, and particularly when I speak
of learning to cluster the objects of perception into similarity sets without
answering questions like, ‘similar with respect to what?’, I am not calling
upon some mystic process to be covered by the label ‘intuition’ and there-
after left alone. On the contrary, the sort of process I have in mind can
perfectly well be modelled on a computer and thus compared with the
more familiar mode of learning which resorts to criteria rather than to a
learned similarity relationship. I am currently in the early stages of such a
comparison, hoping, among other things, to discover something about the
circumstances under which each of the two strategies works more effectively.
In both programmes the computer will be given a series of stimuli (mod-
elled as ordered sets of integers) together with the name of the class from
which each stimulus was selected. In the criterion-learning programme the
machine is instructed to abstract criteria which will permit the classifica-

REFLECTIONS ON MY CRITICS 275

tion of additional stimuli, and it may thereafter discard the original set
from which it learned to do the job. In the similarity-learning programme,
the machine is instead instructed to retain all stimuli and to classify each
new one by a global comparison with the clustered exemplars it has
already encountered. Both programmes will work, but they do not give
identical results. They differ in many of the same ways and for many of
the same reasons as case law and codified law.

One of my claims is, then, that we have too long ignored the manner in
which knowledge of nature can be tacitly embodied in whole experiences

' without intervening abstraction of criteria or generalizations. Those ex-

periences are presented to us during education and professional initiation
by a generation which already knows what they are exemplars of. By
assimilating a sufficient number of exemplars, we learn to recognize and
work with the world our teachers already know. My main past applica-
tions of that claim have, of course, been to normal science and the manner
in which it is altered by revolutions, but an additional application is worth
noting here. Recognizing the cognitive function of examples may also
remove the taint of irrationality from my earlier remarks about the deci-
sions I described as ideologically based. Given examples of what a scienti-
fic theory does and being bound by shared values to keep doing science, one
need not also have criteria in order to discover that something has gone
wrong or to make choices in case of conflict. On the contrary, though I
have as yet no hard evidence, I believe that one of the differences between
my similarity- and criteria-programmes will be the special effectiveness
with which the former deals with situations of this sort.

Against that background return finally to the problem of theory-choice ~
and the recourse offered by translation. One of the things upon which the
practice of normal science depends is a learned ability to group objects and
situations into similarity classes which are primitive in the sense that the
grouping is done without an answer to the question, ‘similar with respect to
what?’ One aspect of every revolution is, then, that some of the simi-
larity relations change. Objects which were grouped in the same set before
are grouped in different sets afterwards and vice versa. Think of the sun,
moon, Mars, and earth before and after Copernicus; of free fall, pendular,
and planetary motion before and after Galileo; or of salts, alloys, and a
sulphur-iron filing mix before and after Dalton. Since most objects within
even the altered sets continue to be grouped together, the names of the sets
are generally preserved. Nevertheless, the transfer of a subset can crucially
affect the network of interrelations among sets. Transferring the metals
from the set of compounds to the set of elements was part of a new theory
of combustion, of acidity, and of the difference between physical and

276 THOMAS 8S. KUHN

chemical combination. In short order, those changes had spread through all
of chemistry. When such a redistribution of objects among similarity sets
occurs, two men whose discourse had proceeded for some time with
apparently full understanding may suddenly find themselves responding
to the same stimulus with incompatible descriptions or generalizations.
Just because neither can then say, ‘I use the word element (or mixture,
or planet, or unconstrained motion) in ways governed by such and such
criteria’, the source of the breakdown in their communication may be
extraordinarily difficult to isolate and by-pass.

I do not claim that there is no recourse in such situations, but before
asking what it is, let me emphasize just how deep differences of this sort
go. They are not simply about names or language but equally and insepar-
ably about nature. We cannot say with any assurance that the two men
even see the same thing, possess the same data, but identify or interpret it
differently. What they are responding to differently is stimuli, and stimuli
receive much neural processing before anything is seen or any data are
given to the senses. Since we now know (as Descartes did not) that the
stimulus-sensation correlation is neither one-to-one nor independent of
education, we may reasonably suspect that it varies somewhat from com-
munity to community, the variation being correlated with the corres-
ponding differences in the language-nature interaction. The sorts of com-
munication breakdowns now being considered are likely evidence that the
men involved are processing certain stimuli differently, receiving different
data from them, seeing different things or the same things differently. I
think it likely myself that much or all of the clustering of stimuli into
similarity sets takes place in the stimulus-to-sensation portion of our
neural processing apparatus; that the educational programming of that
apparatus takes place when we are presented with stimuli that we are told
emanate from members of the same similarity class; and that, after pro-
gramming has been completed, we recognize, say, cats and dogs (or pick
out forces, masses, and constraints) because they (or the situations in which
they appear) then do, for the first time, look like the examples we have
seen before.

Nevertheless, there must be recourse. Though they have no direct
access to it, the stimuli to which the participants in a communication
breakdown respond are, under pain of solipsism, the same. So is their
general neural apparatus, however different the programming. Further-
more, except in a small, if all-important, area of experience, the pro-
gramming must be the same, for the men involved share a history (except
the immediate past), a language, an everyday world, and most of a scientific
one. Given what they share, they can find out much about how they differ.

REFLECTIONS ON MY CRITICS 277

At least they can do so if they have sufficient will, patience, and tolerance
of threatening ambiguity, characteristics which, in matters of this sort,
cannot be taken for granted. Indeed, the sorts of therapeutic efforts to
which I now turn are rarely carried far by scientists.

First and foremost, men experiencing communication breakdown can
discover by experiment—sometimes by thought-experiment, armchair
science—the area within which it occurs. Often the linguistic centre of the
difficulty will involve a set of terms, like element and compound, which
both men deploy unproblematically but which it can now be seen they
attach to nature in different ways. For each, these are terms in a basic
vocabulary, at least in the sense that their normal intra-group use elicits no
discussion, request for explication, or disagreement. Having discovered,
however, that for inter-group discussion, these words are the locus of
special difficulties, our men may resort to their shared everyday vocabu-
laries in a further attempt to elucidate their troubles. Each may, that is,
try to discover what the other would see and say when presented with a
stimulus to which his visual and verbal response would be different. With
time and skill, they may become very good predictors of each other’s
behaviour, something that the historian regularly learns to do (or should)
when dealing with older scientific theories.

What the participants in a communication breakdown have then found
is, of course, a way to translate each other’s theory into his own language
and simultaneously to describe the world in which that theory or language
applies. Without at least preliminary steps in that direction, there would
be no process that one were even attempted to describe as theory-choice.
Arbitrary conversion (except that I doubt the existence of such a thing in
any aspect of life) would be all that was involved. Note, however, that the
possibility of translation does not make the term ‘conversion’ inappropriate.
In the absence of a neutral language, the choice of a new theory is a deci-
sion to adopt a different native language and to deploy it in a correspond-
ingly different world. That sort of transition is, however, not one which
the terms ‘choice’ and ‘decision’ quite fit, though the reasons for wanting
to apply them after the event are clear. Exploring an alternative theory by
techniques like those outlined above, one is likely to find that one is already
using it (as one suddenly notes that one is thinking in, not translating out of,
a foreign language). At no point was one aware of having reached a deci-
sion, made a choice. That sort of change is, however, conversion, and the
techniques which induce it may well be described as therapeutic, if only
because, when they succeed, one learns one had been sick before. No
wonder the techniques are resisted and the nature of the change disguised
in later reports.

278 THOMAS 8S. KUHN

REFERENCES

Brown [1969]: ‘The Electric Current in Early Nineteenth-Century French Physics’,
Historical Studies in the Physical Sciences, 1, pp. 61-103.

Cavell [1969]: ‘Must We Mean What We Say?’, in Must We Mean What We Say?, pp. 1-42.

Gombrich [1960]: Art and Illusion, 1960.

Heilbron and Kuhn [1969]: “Che Genesis of the Bohr Atom’, Historical Studies in the
Physical Sciences, 1, pp. 211-90.

Klein [1964]: ‘Einstein and the Wave-Particle Duality’, The Natural Philosopher, 3, pp. 1-49.

Kuhn [1962a]: The Structure of Scientific Revolutions, 1962. [A second edition, revised and
enlarged by a new chapter entitled ‘Postscript 1969’, is to be published as a Phoenix
paperback by Chicago University Press in 1970.]

Kuhn [19626]: ‘The Function of Measurement in Modern Physical Science’, Isis, 52, pp.
161-93.

Kuhn [1964]: ‘A Function for Thought Experiments’, in Cohen and Taton (eds.): Mélanges
Alexandre Koyré, Vol. 2, L’aventure de l’esprit, pp. 307-34.

Kuhn [1969]: ‘Comment [on the relations between science and art]’, Comparative Studies
in Philosophy and History, 11, pp. 403-12.

Kuhn [1970]: ‘Second Thoughts on Paradigms’, in Suppe (ed.): The Structure of Scientific
Theory, 1970.

Nida [1964]: ‘Linguistics and Ethnology in Translation-Problems’, in Hymes (ed.):
Language and Culture in Society, pp. 90-7.

Popper [1963]: Conjectures and Refutations, 1963.

Quine [1960]: Word and Object, 1960.

Raman and Forman [1969]: ‘Why Was It Schrédinger Who Developed de Broglie’s
Ideas?’, Historical Studies in the Physical Sciences, 1, pp. 291-314.

Schagrin [1963]: ‘Resistance to Ohm’s Law’, American Journal of Physics, 31, pp. 536-7.

Scheffler [1967]: Science and Subjectivity, 1967.

Shapere [1964]: ‘The Structure of Scientific Revolutions’, Philosophical Review, 73,
Pp. 383-94.

Shapere [1966]: ‘Meaning and Scientific Change’, in Colodny (ed.): Mind and Cosmos:
Essays in Contemporary Science and Philosophy, 1966, pp. 41-85.

Toulmin [1967]: ‘The Evolutionary Development of Natural Science’, American Scientist,
55, Pp. 456~71.

Name Index*

Agassi, 30, 36n, 113n, 115n, 123n, 128m,
131n, 184

Agassiz, 42-3, 44, 47

d’Alembert, 142

Ampére, 251

Angstrom, 50

Aristotle, 36, 62, 99, 227, 265

Austin, 201n

Ayer, 181

Balmer, 147, 148, 150n, 152, 156, 159,
246, 257

Bartley, 182n

Barus, 85n

Becke, 172n

Beckman, g1n

Bellarmino, 188, 189n

Bergson, 188

Berkeley, 55

Bernal, 162n

Bernard, 117n

Bernoulli, 273

Bernstein, 174n

Bethe, 172n

Black, 80, 85

Blokhinzev, 145n

Bohm, 145n, 206, 22In, 224n, 246

Bohr, 91, 115, 124, 137n, 138, 140-54,
156, 159, 166, 168-72, 174, 221n,
224n, 246, 251, 256-9

Bolingbroke, 50

Boltzmann, 54, 167, 208, 211

Bondi, 221n

Born, 144n, 150-1, 153n, 161n

Bose, 167

Bothe, 169

Boyle, 147n

Brace, 161n

Brackett, 147

Bragg, 166

Brahe, 6, 9, 152n

Braithwaite, 16n, 97, 109n, 113n, 114n

Brecht, 228n

Brentano, 99n

Brinton, 45

Brodbeck, 81n

de Broglie, 754, 183n, 258, 259

Brown, 251n

Bruner, 64
Brunswick, g9n
Burge, 269n
Burtt, 92, 183n

Cajori, 136n

Callendar, 166, 167n

Campbell, D., 99n

Campbell, N., 77, 78

Canfield, 186n ye

Carnap, 92n, 95n, 113n, 178, 183n, 222,
225, 234, 270

Carnegie, 200n

Carnot, 166

Cavell, 237n

Chadwick, 168, 169n, 170n

Chwolson, 163n

Clark, viii

Coffa, 186n

Collingwood, 40

Comte, 183n

Compton, 169, 258, 259

Conring, 123

Copernicus, 6, 10, 36, 275

Cotes, 145

Coulomb, 254

Crombie, 39n

Crookes, 139

Cullen, 152

Cuvier, 42-3, 45

Dalton, 255, 269, 275

Darwin, C., 42, 45, 54

Darwin, C. G., 256

Davisson, 147n, 154

Debye, 49, 153n

Descartes, 65, 97, 99, 147n, 152n, 158,
227, 276

Dillinger, 200

Dirac, 164n, 171, 172

Doppler, 226

Dorling, 164n

Dreyer, 117n

Duhem, 30, 36, 91, 105-6, 117, 123n,
134, 180, 183n, 784-6

Eccles, 181n
Eddington, 222n

* Italic page numbers denote the more important references,

279

280 NAME INDEX

Ehrenfest, 153n, 164n, 167n, 169n

Einstein, 5, 6, 44, 57, 72, 92, 97, 103,
rosn, I13n, I2In, 124, 142-6, 147,
149, 150, 153N, 157, 159, 162, 163-5,
167, 174, 183n, 206, 208, 212n, 224n,
246n, 2575 258-9, 265

Ellis, 168, 1770

Engels, 211

Epstein, 199n

Euler, 147n, 152n

Evans, 148n

Faraday, 50, 183n, 207

Feigl, 57n, 225

Fényes, 145n

Fermi, 170-2

Feyerabend, vii, 25, §7n, 60, 67-8, 71n,
80, 81n, 93n, I07n, 115n, Trg9M, 122N,
124n, 131, 136n, Z45n, r50n, 155,
178n, 179m, 187n, 197-230, 231, 232,
233, 234, 235, 236, 237, 245, 246, 254,
262, 263, 266, 268, 269n

FitzGerald, 161n, 162, 763

Flamsteed, 130n

Fodor, 82n

Forman, 258n

Fowler, 148~9

Frank, 53

Franklin, 62, 63

Fresnel, 159-62, 165n

Fries, 99n

Gale, 164n

Galileo, 98, 100n, £07, 115, 117, 124;
142, 173, 188, 21 4n, 227, 254, 273,275

Gamow, 165n, 169

Gardner, 165

de Gaulle, 263n

Geiger, 169

Germer, 154

Gombrich, 228n, 244n, 262n

Good, 87n

Goudsmit, 153, 154n

Grandy, 231n

Gray, 63

Gregory, 76n

Grinbaum, 162n, 187

Guerlac, 5n

Hafner, 5n

Halley, 31

Hattiangadi, 25

Hawkins, 20n

Hegel, r04n, 198, 209n, 213

Heilbron, 256n

Heisenberg, 145, 164n, 169, 170n, 171,
172

Helmholtz, 159

Hempel, 14n, 173, 183n, 225n, 231n

Henderson, 170

Hero, 146

Hertz, 207

Hesse, 77> 78, 83

Hevesy, 142n, 149n

Hooke, 36, 136

Howson, gin, 186n, 197n

Hume, 175n, 178

Hund, 150n

Hutton, 42

Huyghens, 145, 158, 187n, 273

Jacobson, 171

Jaffe, 164n

James, 99n, 185, 188
Jammer, 147n, 154n
Janossy, 145n

Jeans, 165, 166
Jevons, 80

Joffé, 167n

Jones, viii

Juhos, 181n

Kant, 51, 72, 94n, 98n, 99, 100n, r04,
188n

Katz, 82n

Kelvin, 161, 162n

Kepler, 9, 3o-I, 36, 135, 147n, I52n,
158, 255

Keynes, 123, 124n

Kilmister, 91n

Klein, 258n

Kneale, vii

Koestler, 117n

Konopinski, 172n

Korn, 166

K6rner, vii

Koyré, 92n, 183n, 187n

Kramers, 125, 144n, 153n, 168, 170-1

Kronig, 154

Kudar, 170n

Kuhn, S., 269n

“Kuhn, T. S., vii, 1-23, 25-37, 39-42,

43-7, 49-59, 51-8, 59-71, 72-7) 79,
80, 82-5, 87-8, 92-3, 115, 135» 155,
159, 177-80, 189n, 197-203, 204,
205-7, 208, 209, 210, 2r1~14, 216,
218, 219, 231-78

Kiulpe, 99n

NAME INDEX 281

Lakatos, vii, 13-14, 25, 44, 60, 91-196,
202, 203n, 204, 205n, 211-16, 218,
224N, 229, 231, 233, 235, 237-41, 245,
246, 247, 256-9, 262, 267

Landé, 145n, 153

Laplace, 133n, 252

Larmor, 161n, 166

Laudan, gin, 187n

Laue, 144

Lavoisier, 5, 62, 64, 251

Leader, gin

Lee, 5

Lehrer, 186n

Leibnitz, 123, 187n, 188

Lenin, 205n, 211

Le Roy, 104-5, 176, 185n, 188

Levi, 203n

Lewis, 185

Lorentz, 6, 141, 142, 159n, 160-5, 166,
204n, 226, 256

Love, 166

Lummer, 91, 159, 165-7

Lyell, 42, 45, 62

Lykken, 176n

Lyman, 147

Lysenko, 263

Mach, 55, 162, 211

MacLaurin, 147n

Margenau, 142, 145n, 154n

Marignac, 139

Marx, 228n

Marzke, 221n

Masterman, vii, 49, 59-90, 231, 233, 234,

243, 271, 272N, 273

Maxwell, G., 57n

Maxwell, J. C., 54, 103, 115, 139N, I41,

142, 146, 167, 183n, 207, 208, 256

McCormick, viii

McCulloch, 152n

Medawar, 96n, 181n

Meehl, 175n, 176n

Meitner, 168, 170

Mendeleev, 257

Michelson, 91, 150, 152n, 159-65, 204n,
226

Milhaud, 104, 105n

Mill, 94n, 98n, 123, 211

Miller, 162n, 163n, 165, 204n

Moliére, 117n

Morley, 91, 159-65, 204n, 226

Moseley, 150

Moszkowski, 172n

Mott, 170

Musgrave, vii, g1n, 92, 182n

Nagaoka, 256

Nagel, 173n, 181n, 225

Needham, 85n

Neurath, 173-4, 156n

Newton, 30-1, 39-40, 55, 57, 62, 71-2,
97, T00-T, 103, 104n, 105n, Tz0—r,
115, 117N, 121n, 124, 126, 130n, 131n,
133, 135-6, 145, 147n, 155n, 156n,
158-9, 173, 183, 187n, 202n, 208, 254,
255, 265, 272-3

Neyman, 1o9n

Nicholson, 148n, 257

Nida, 269n

Ohm, 251
Olschki, 214n
Orthmann, 168n

Parker-Rhodes, 85n

Pascal, 94n

Paschen, 147

Pasteur, 54

Pauli, 137n, 153, 168n, 169-70, 171

Pearce Williams, vii, 49—50, 54, 57, 161n,
252

Pearson, 109n

Peierls, 171, 172

Pfund, 147

Piaget, 223, 224n

Pickering, 148

Planck, 50, 54, 141, 144, 147, 150, 1§3n,
154, 165-7, 175n, 203n, 257, 258-9

Plato, 6, 180, 218

Podolski, 224n

Poincaré, 104-5, 134, 208

Poisson, §7, 254

Polanyi, 92, 115, 163n, 178

Popkin, 94n

Popper, vii, 7-8, 10-16, 19, 21-2, 25-6,
28-9, 31, 32, 34, 36-7, 39, 40, 45, 46,
49-50, 51-8, 60, 61n, 67, 68, 71-2, oI,
92-3, 94n, 95, 96n, 97, 98n, 99, Toon,
101N, Io2n, 104N, 105-77, 119n, 121Nn,
122n, 123, 124,126, 127n, 128n, 131n,
132, 133n, 144M, 145N, 154, 155, 156,
158n, 159n, 162n, 165n, 169n, 174n,
175n, 176-84, 186n, 88-9, 197n,
206n, 211, 212, 216-9, 228, 231, 232,
233, 234-5, 237, 238, 242-6, 247-8,
252, 253-5, 261, 264-6, 267, 271

Post, vii

Postman, 64

282

Potier, 164

Pound, 228

Power, 146n

Poynting, 166

Presswood, 5n

Priestley, 64, 251, 260
Pringsheim, 91, 159, 765-7
Prokhovnik, 164n

Prout, 91, 128, 137n, 138-40, 141, 142
Ptolemy, 9, 62

Putnam, 81n, 82n, 203n

Quine, 82n, 91, 180, 184-6, 188, 268-9

Rabi, 164n

Raman, 258n

Rayleigh, 161n, 164, 165, 166

Reagan, 198n

Reichenbach, 136n, 234

Rosen, 224n

Rosenfeld, 221n

Rosseland, 153n

Rousseau, 188n

Runge, 164n

Russell, g5n, 113n, 188

Rutherford, 139, 141, 147, 166, 170n,
256—7

Rydberg, 148n, 149n

Ryle, 81n

Salmon, 187

Schagrin, 251n

Scheele, 251

Scheffler, 261n, 269n

Schilpp, 1n

Schlick, 51

Schrédinger, 143n, 145n, 164n, 169,
172n, 183n, 258

Schumacher, 224n

Schwarzschild, 153n

Scriven, 81n

Shankland, 164n, 171, 172

Shapere, 34n, 254n, 261n, 266n

Simon, 169

Sitte, 172n

Slater, 125, 168, 170-1

Smoluchowski, 157

Sneath, 86n

Soddy, 137n, 139n, 140

Sokal, 86n

Sommerfeld, 142n, 149-50, 153, 251

Sparck-Jones, 85n

NAME INDEX

StahIman, 8n

Stas, 128, 139
Stebbing, 188
Stegmiiller, 186n
Stokes, 159-60, 162-3
Strawson, 82n

Stroud, 223n

Sukale, 91n

Sukarno, 25, 26

Synge, 165, 221n, 226n

Tanimoto, 86n

Tarski, 56, 265

Ter Haar, 153n, 166n, 167n

Thales, 6

Thompson, 50

Thomson, 166, 170n, 256

Thorndike, 8n, 9n

Toulmin, vii, 39-47, 81n, 180n, 231,
233, 241, 249-50, 267

Treiman, 173n

Trotsky, 205n, 211

Trouton, 161n

Truesdell, 136n

Tyndall, 50

Uhlenbeck, 153, 154n, 172n

van der Waerden, 168n

Watkins, vii, 25-38, 60n, 61, 75, gin,
Q3n, Ilan, 132, 133n, 161n, 178, 184,
222N, 231, 233, 235, 236, 241-2, 246,
247-8, 254-5, 266

Weyl, 96, 208

Wheeler, 26n, 221n

Whewell, roon, 104, 105n, 123n, 124n,
126n, 147, 188

Whittaker, 144, 161n

Wien, 165, 166, 167n, 208

Wilson, 153n

Wisdom, vii, 112n, 141n

Wittgenstein, 53n, 198

Wohlwill, 214n

Wooster, 168n

Worrall, viii, gin, 197n

Wu, 169n, 172n

Yang, 5
Young, 146, 159

Zeeman, 257, 258

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